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Wednesday, February 06, 2019

Why a larger particle collider is not currently a good investment

LHC tunnel. Credits: CERN.

That a larger particle collider is not currently a good investment is hardly a controversial position. While the costs per units of collision-energy have decreased over the decades thanks to better technology, the absolute cost of new machines has shot up. That the costs of larger particle colliders would at some point become economically prohibitive has been known for a long time. Even particle physicists could predict this.

Already in 2001, Maury Tigner, who led the Central Design Group for the (cancelled) Superconducting Super Collider project, wrote an article for Physics Today asking “Does Accelerator-Based Particle Physics Have a Future?” While he remained optimistic that collaborative efforts and technological advances would lead to some more progress, he was also well aware of the challenges. Tigner wrote:

“If we are to continue progress with accelerator-based particle physics, we will have to mount much more effective efforts in the technical aspects of accelerator development — with a strong focus on economy. Such efforts will probably not suffice to hold constant the cost of new facilities in the face of the ever more demanding joint challenges of higher collision energy and higher luminosity. Making available the necessary intellectual and financial resources to sustain progress would seem to require social advances of unprecedented scope in resource management and collaboration.”

But the unprecedented social advances have not come to pass, and neither have we since seen major breakthroughs in collider technology. The state of affairs is often summarized in what is known as the “Livingston Plot” that shows the year of construction versus energy. You can clearly see that the golden years of particle accelerators ended around 1990. And no game-changing technology has come up to turn things around:

Particle accelerators are just damn expensive. In the plot below I have collected some numbers for existing and former colliders. I took the numbers from this paper and from Wikipedia. Cost estimates are not inflation-adjusted and currency-conversions are approximate, so do not take the numbers too seriously. The figure should, however, give you a roughly correct impression:

The ILC is the (proposed) International Linear Collider, and the NLC was the once proposed Next Linear Collider. The SSC is the scraped Superconducting Super Collider. FCC-ee and FCC are the low-cost and high-cost variants of CERN’s planned Future Circular Collider.

When interpreting this plot, keep in mind that the cost for the LHC was low because it reused the tunnel of an earlier experiment. Also note that most of these machines were not built to reach the highest energies possible (at the time), so please do not judge facilities for falling below the diagonal.

So, yeah, particle collider are expensive, no doubt about this. Now, factor in the unclear discovery potential for the next larger collider, and compare this to other experiments that “push frontiers,” as the catchphrase has it.

There is currently no reason to think a larger particle collider will do anything besides measuring some constants to higher precision. That is not entirely uninteresting, of course, and it’s enough to excite particle physicists. But this knowledge will tell us little new about the universe and it cannot be used to obtain further knowledge either.

And that is even though the scientific case for LIGO was clear. Gravitational waves were an excellently solid prediction. Not only this, physicists knew already from indirect measurements that they must exist. True, they did not know exactly at which amplitude to expect events or how many of them. But this was not a situation in which “nothing until 15 orders of magnitude higher” was the most plausible case.

In addition, gravitational waves are good for something. They allow physicists to infer properties of distant stellar objects, which is exactly what the LIGO collaboration is now doing. We have learned far more from LIGO than that gravitational waves exist.

The planned FCC costs 20 times as much, has no clear discovery target, and it’s a self-referential enterprise: A particle collider tells you more about particle collisions. We have found the Higgs, all right, but there is nothing you can do with the Higgs now other than studying it closer.

Another cost-comparison: The Square Kilometer Array (SKA). Again the scientific case is clear. The SKA (among other things) would allow us to study the “dark ages” of the universe, that we cannot see with other telescopes because no stars existed at the time, and look for organic compounds in outer space. From this we could learn a lot about star formation, the mystery that is dark matter, and the prevalence of organic chemistry in the universe that may be an indicator for life. The total cost of the SKA is below $2 billion, though it looks like the full version will not come into being. Currently, less than a billion of funding is available that suffices only for the slimmed-down variant (SKA-1).

And it’s not like building larger colliders is the only thing you can do to learn more about particle physics. All the things that can happen at higher energies also affect what happens at low energies, it’s just that at low energies you have to measure very, very precisely. That’s why high-precision measurements, like that of the muon g-2 or the electric dipole moment, are an alternative to going to higher energies. Such experiments are far less costly.

There are always many measurements that could be done more precisely, and when doing so, it is always possible that we find something new. But the expected discovery potential must play a role when evaluating the promises of an investment. It is unsurprising that particle physicists would like to have a new particle collider. But that is not an argument for why such a machine would be a good investment.

Particle physicists have not been able to come up with any reliable predictions for new effects for decades. The prediction of the Higgs-boson was the last good prediction they had. With that, the standard model is complete and we have no reason to expect anything more, not until energies 15 orders of magnitude higher.

Of course, particle physicists do have a large number of predictions for new particles within the reach of the next larger collider, but these are really fabricated for no other purpose than to rule them out. You cannot trust them. When they tell you that a next larger collider may see supersymmetry or extra dimensions or dark matter, keep in mind they told you the same thing 20 years ago.

202 comments:

I dare predict that regardless of how many facts and solid arguments you bring to bear, this will shortly derail again into ad hominems. So, for what it's worth, I do believe it is important to speak up and you're doing a great job at that, regardless of whether one agrees or if it ultimately results in change.

On a different note, since it fits better under this article, I'd like to iterate an argument made below your last post.

Assume that one completely agrees with your analysis that money could be better spent elsewhere. Also assume that resource allocation in societies does not always work in what one might dub "rational". Undoubtedly, the proposed FCC DOES have a certain amount of value.What it boils down to then is the hope that not building the FCC will funnel the money into other ventures that collectively, have larger benefit, either to science (if you want to be stringent) or otherwise to society in general.

I'm probably a cynicist I guess, but I'm not sure about that. I think it equally possible that the money goes towards military spending or ends up as a reduced VAT for hoteliers (as was the case some years ago ;)

Bottom line, I'm no longer sure that it is possible to actually make an optimal decision for oneself on what opinion to hold. Anyway, more information helps and you're one source of that, so keep on going :)

„I think it equally possible that the money goes towards military spending or ends up as a reduced VAT for hoteliers (as was the case some years ago ;)“

Do I get you right here? Your argument goes something like this: It’s ok to spend public money for a likely useless thing and the reason for that being ok is, that it might otherwise be spent for another likely useless thing. Great, we are doomed.

This is a very good point! We could, for good reasons, turn away from high energy colliders. This from considering that the probability is low of being good value.

However, humans being humans we may well spend money on something with even less to show for it at the end of it. Space probes and expensive observatories that "map" Dark Matter "distribution". I cringe at the thought of such a waste of human resources.

Voter's are subject to emotion and trust, rather than logic and probability. If they do not take it on the authority of one set of Scientists, they are likely to still take it on some scientists authority, rather than the logic and probability of it being fruitful...

Since scientists are voters, following your statement I deduce that scientists are also „subject to emotion and trust, rather than logic an probability“. I totally agree since both, the population of scientists and the population of voters habe mammalian brains.

Smaller experiments like the muon g-2 and the electron dipole moment measurements are important and should be done. But it’s misleading to characterise them as alternatives to going to higher energies. The two approaches are complementary, not replacements for each other. Low energy precision experiments make a single specific measurement very precisely, sensitive to a very particular type of new physics. Colliders are more general purpose machines that make thousands of measurements. Both approaches are necessary for full visibility. Blinding one eye won’t make the other sharper.

I've been wondering why I can't get fully on board with your position here, and it finally hit me: You're advocating that we don't look, and that's a position I just can't get behind.

Is it massively wasteful and silly? Yes. Are we likely to find anything new? Highly unlikely. (But, AIUI, we will learn more details about things.) Is there good reason to build it? Probably not really.

But, I'm sorry, we still have to look. Isn't that what science is all about? Looking?

You are misunderstanding. The question is not "look or don't look" it's "where do we look". I am saying, we currently have more promising avenues to pursue. Building a larger particle collider is currently not the best way to invest into progress in the foundations of physics. Look closer at dark matter, scrutinize any of the existing anomalies, focus on quantum gravity or quantum foundations. All these are less costly and more promising avenues. I am sure if you ask people in disciplines other than particle physics they will have their own examples to add.

Can we (to give people something new to build that isn't a 100 kilometer loop) build a detector at CERN that can investigate the near field, at, say, scales of nanometers to attometers, instead of the far field S-matrix, at the characteristic scales of centimeters to dekameters of ATLAS and CMS? That would need the bunches to be *much* smaller than presently and for the detectors to measure and analyze field observables of the beam instead of or as well as particle observables.Of course this comes from a very different perspective from all the theory you discuss in your book and here, a perspective that isn't yet well enough developed to tell us that there's anything at all to see in the near field that can't be seen in the far field (so I'm suggesting we look elsewhere just to what there is, precisely what you denounce when it comes from other theorists), but taking near-field observables more seriously is something for theory people to do that isn't just looking for more particles, and it seems like experimentalists might find it fun to design new kinds of detectors.

For the sake of saving time, allow me to caricature the argument on the other side by quoting the ever-reasonable Phillip Helbig:

"In the grand scheme of things, the amount of money is peanuts. Probably more is spent on tattoos and piercings. It is silly to argue against a project because it sounds expensive when one quotes the price tag being borne by dozens of countries over a few decades."

Sabine wrote: Now, factor in the unclear discovery potential for the next larger collider.

Phillip has an answer to that point too:

"I don't see the lack of expectation as a reason not to build it."

As far as I know, I'm the only person who offered a serious rebuttal to Phillip's "peanuts" argument, but he didn't respond.

Is there anyone in this blog who wants to do more than post talking points?

The annual cost of CERN, at about 1 Billion CHF, is equal to 2 cappucinos per inhabitant of the member states. The price for a new collider would not have to be paid upfront, but it woyld be built at constant budget (as did LHC and currently High-Luminosity LHC). The high spending during construction is covered by loans, which are repayed from the (constant) budget over the following years of exploitation.

Ah, yes, the "it's only so-and-so many cents per day per person" argument. You realize you can do the same exercise with literally any other expense and it doesn't make it any cheaper? Also, I have debunked this silly argument dozens of times already. Try harder.

Sabine, the fact that you disagree with an argument does not mean that it is invalid ("debunked").Taxpayers, to whom we are in fine liable, may want to undestand how the money they handed over to the state is used, and some visual comparisons (cents per day or cappucinos per year) help in making abstract numbers understandable. I have nothing against doing the same exercise with other posts in budget, for example cost of education for our children, cost to the society of joblessness, of saving the banks and so on. In the face of some of these numbers, particle physics research would pale, and would make it visible that money _is_ available in our societies, for colliders as well as for foundational expoeriments which will rate at a fraction of a cent per year in this picture.

I do not "disagree" with this argument, I point out that it's stupid. Of course you can divide $20 billions by whatever number of people you wish, there is nothing to disagree here. But that doesn't make it any less expensive. To state the obvious, you can equally well compare total numbers.

LIGO discovered a solid prediction, gravitational waves, made from a well established theory, general relativity. This opens up a new window to observe all kinds of processes of objects in our universe, whether part of the standard cosmological model or beyond it. It would be crazy to shut down that window now just because all it discovered was compatible with general relativity, and argue that there are cheaper ways to learn about what goes on in the universe, like an antenna in a desert that can measure the 21cm signal of cosmic dawn and is also important.

Now the LHC discovered a solid prediction, the Higgs boson, made from a well established theory, the Standard Model. This opens up a new window to observe all kinds of processes of objects that make up our universe, whether part of the standard particle physics model or beyond it. It would be a shame to shut down our most powerful magnifying glass on to the sub-microscopic world in the 21st century, while it is still within the realm of affordability. Smaller precision experiments can and will always be done. But they offer complementary information that only partially overlaps with what colliders can measure and probe.

Whatever theoretical hype may have disappointed you and others in the past, going forwards having more experimental data and windows on to different sectors of nature can only be more beneficial than having less. It is an exciting endeavour to keep looking and understanding nature on all scales, doing the good science of understanding what we see regardless of what exotic things we expect or predict. After all we don’t abandon astrophysics and cosmology because there’s slim prospects of discovering fundamentally new types of stars beyond further understanding existing stellar processes, or because everything is compatible with the standard LambdaCDM. No: we keep gathering data, modelling it, understanding it, and refining our understanding, because that’s what science is about.

In addition to all the processes involving quarks, leptons, W, Z bosons and photons, we can now observe processes involving the Higgs directly as well. These are the objects that make up (part of) our universe.

To begin with it's nonsense to say that the "Higgs allows us to see" particles we have seen before we knew the Higgs is even there. More importantly, as I said, if you look at particles that tells you more about those particles. Certainly true, but not much else you can do with it.

In any case, as I said many times, I certainly think it is interesting to study those particles further, but if I contemplate the use of doing so the potential seems very limited compared to other things we could be doing.

As for the argument about the expense of maintaining this particular window open when shutting it would open up many other windows, this naive argument has been addressed many, many times: science funding for large ambitious projects is not a zero-sum game.

Sorry I’m not sure how what you just said addresses the point that taking money away from particle physics won’t make it reappear in other areas of physics.

Rather, we should think about how to increase money in all these other equally important areas of physics that also deserve more funding. It’s not like we can’t afford it. The taxpayer cost of these large projects equates per person to about a cup of coffee a year; let’s get more cups of coffee going to all areas of science. It’s a drop in the ocean that will hardly bankrupt us.

We don't live in a world of infinite resources. This next collider would be staggeringly expensive compared to the next largest experiment we could conduct. Every decision about what gets funded involves an opportunity cost. Every dollar spent in one way is one less dollar to spend on something different.

You would think people making a living in the sciences would have some basic grasp of economics.

I am not "taking away money" I am pointing out that it's not a good investment.

Ah, here we go again with the the "it's only so-and-so-little per person per day argument." Have you noticed that you can do this with literally any other expense? What kind of argument is that? What is it supposed to show?

"About what the best thing to do is, wouldn't you say that reaching higher energies than we've ever probed before is the most effective way to search for new physics?

No, if you look at the history of physics, breakthroughs have happened when we resolved an inconsistency, either between theory and data or an internal inconsistency in the theory. I conclude that the best way to find new physics is to do what worked in the past. In high energy physics we presently have neither situation. The standard model is complete and it's fine the way it is and unless the LHC brings up something unexpected (which can certainly still happen), there's no good reason to look further.

Again, the cost comparison is important when your argument is that A is too expensive, we should rather be funding better-value-for-money B. First, not investing in A won't make money appear in B. Second, A is only expensive relative to B but it's important to contextualise the scary-sounding numbers. Third, apart from the g-2, electron dipole moment, and quantum experiment examples, you have yet to give specific examples of actual experiments that would make up your programme B. What is your concrete proposal for B exactly?

The options within A are being discussed, but if we don't do colliders the pot of money is reduced and we simply won't have a collider. There is no magical scenario where the extra billions go into thousands of million dollar experiments. Even if it could, you can't concretely demonstrate a better physics case than the thousands of guaranteed measurements of all kinds of Standard Model processes opened up by a collider, in addition to its pure discovery potential.

Besides, your logic that the Standard Model is complete so there's no good reason to look further applies to low-energy precision measurements that are also just making Standard Model measurements. The foundations of quantum mechanics are on even more solid footing, so your vague suggestion to put money into testing that instead also appears to be contradictory with your logic.

Finally, it seems we just have to agree to disagree on whether A is worth doing at all, irrelevant of comparisons with B. Although from your quote above it appears you also have to agree to disagree with yourself.

That's right, I changed my mind about building a larger collider because I realized I am not consistent with myself when being in favor of it. I think it is correct that looking at higher energies is the cleanest way to probe short distances but it's not the only way. More importantly though, I don't think it's currently promising to probe higher energies/shorter distances.

The foundations of quantum field theory are far from being on solid footing. There are lots of unsolved problems there that receive very little attention. Also, if you think the foundations of quantum mechanics are "on solid footing" you basically missed the last 100 years.

But really this isn't the point. I don't expect you (or anyone else for that matter) to sign up to my argument for why dark matter, quantum gravity, quantum foundations are the most promising experimental avenues. But at least *I* have an argument. Which is more than can be said about anyone else. Particle physicists' only argument is basically that they think particle physics is interesting. That does little to explain why a larger particle collider is a good investment.

What is the meaning of the cost vs. energy plot? Why not cost vs. luminosity or luminosity per energy consumption ?What does the term 'cost' include? Again I couldn't find this in the paper that you cite.

As you probably know XFEL, ESS are not colliders so I am not sure why they are in the same plot while SSC, TESLA were not built.

What does 'FCC' stands for at the right top? Do you refer to a combined FCC-ee + FCC-hh programme? Does it include the HE-LHC upgrade?

I am surprised not to see any cost uncertaintie (error bars) in this plot.

Yes, I made the plot. As I said, I took the numbers from Shiltsev's paper and from Wikipedia. I also said that you shouldn't take the amounts too seriously. These are in the plot simply because they're in Shiltsev's list and I copy&pasted this, that's all. (I removed some points because they laid on top of other points.)

FCC is the full program, in my understanding that includes the FCC-ee prestage.

(projected) is there simply to say that it's the com energy some of those are supposed to deliver or were supposed to deliver rather than actually delivering or having delivered.

If you want to instead plot something else, please do not hesitate to do so.

The mistakes made in this argument by Sabine are economic and not scientific. If money is not spent on a larger collider then that money will be spent elsewhere... maybe another war.

The global economies are already spending more than available, so adding 20B to this debt does nothing. The potential gain from a new collider verses gains from other ways to waste the money are obvious. Even if no new particle physics is found, the discoveries and improvements of building a new technology will be worth whatever is spent.

As I have said many times, the existence of stupidity does not justify more stupidity. Just because money is wasted in one place doesn't give scientists permission to waste it in other places.

Do you people even realize that you are basically arguing that, yes, a larger collider is a waste of money but, hey, give us $20 billion anyway? What the heck do you think you will achieve with that other than making scientists look like total idiots?

Yes it does. The money is going to be wasted. This is a chance it will do good.

You are trying to make sense of a financial system that makes no sense. If you don't spend it and expect it to be there in a few years for other uses, then you are a fool. The central banks of the world are using money now to hold up stock markets. This will fail and that money will be gone.

At the minimum, the 20B will employ scientist who will discover all sorts of things. This is the whole concept of the military industrial complex. Does it make sense to spend all that money on defense. No. But significant scientific breakthroughs have occurred with this "wasted" money.

In 50 years someone will ask, "why didn't we build a larger collider?" Do you want to be remembered as a wise scientist or a clueless practitioner of economics?

"Do you people even realize that you are basically arguing that, yes, a larger collider is a waste of money but, hey, give us $20 billion anyway?"

One last comment. You are acting as if $20B is a large number. It is a 20 dollar bill in context of the trillions wasted every year to prop up the stock markets and pay politicians and company executives. You will regret this stand in 10-20 years when you begin understand what could have been accomplished with a $20 bill.

The problem with high-precision experiments, to indirectly measure high-energy scales at low energies, is that they require a very high level of precision, which means high luminosity and optimization of the detectors in such a way that the explored space of the parameters is smaller with respect to a high energy collider.See, e.g., slide 9 of this presentation https://indico.cern.ch/event/753671/contributions/3272998/attachments/1783851/2903353/CLICws-1-2019.pdfAlso, all these high-precision experiments still try to probe the same class of models as new particle colliders.If all predictions based on naturalness are flawed (irrespective of the merit of a specific model), then all experiments testing these models are waste of money.Actually, except for neutrinos, all particle physics experiments are useless, since they all try to find physics beyond the standard model, which is usually based either on naturalness arguments (SUSY, axions, etc) or on numerical coincidences (dark matter).

The comments about the technological advancements not being enough to allow cheaper higher energy colliders is also moot, as most of the advancements in super-conducting magnets, high temperature magnets, plasma wakefield acceleration, and so on are driven by the need of reaching better performances in terms of collision intensity and energy.Sure, there are other fields in science which are investing in these technologies, but if you kill high energy colliders the funding for these type of applied research will go down for sure, slowing the pace of innovation.

Another thing: speaking of absolute cost is pointless, as all proposed colliders have a lifetime of the orders of decades, in order to maximize the return of physics.Obviously, colliders are the most expensive experiments, but it's one thing to say "20 billions of euros!" versus "1 euro per person per year for 20 years for everybody in Europe"...

"...all proposed colliders have a lifetime of the orders of decades,..." That's right, to get ROI, the collider will have to operate for 30∼40 yrs. But after the first 5∼10 yrs, when in all likelihood, it becomes apparent that there's nothing new to see, theorists will pack it in, add another zero to their predictions, and go on to something else. Experimenters (mostly young people) will be tasked with spending their careers playing it all out (as is now happening at the LHC). Great for job security, but not much of a career.

I am a recent "dropout" from the technology side of the HEP particle collider, more specifically, superconducting magnets. As an experienced veteran in the field, a comment I can add here is that the technical outlook of building any hadron circular collider with energy significantly higher than current LHC is rather dim.

There are several key reasons for this

The first is that high field collider magnets are extremely challenging to design and fabricate. Helium cryogenic, high current, 10^-4 field uniformity, high internal stress, radiation damage. Any one of these is already complicated enough. Collider magnet, unfortunately, is a combo of all. With current material/technology, 100 Tev machine is almost impossible.

Argument is that hope may be with more advanced superconductor technology. Well, here comes a even bigger problem: the lack of a truly mature industry to support it. This is because superconducting wires that can meet the need of building stronger collider barely have other application and no real market. Many of the manufacturers of these wires have closed their door and the few ones that survive are considering to abandon this "business". In some recent scenario, it feels so miserable that some HEP funding agencies need to persuade/beg these manufacturers to stay. An example commonly cited by HEP community to prove the economical benefit from collider technology development is the successful incubation/creation of the MRI market. Honestly, this is a time-sensitive argument of which the validity is questionable in the 2010-2020 age. It is true that current MRI relies on NbTi wires that were initially developed for collider magnets and these wires are the backbone of Tevatron and LHC magnets. On the other hand, the ~8 T which NbTi magnets can generate is more than enough for commercial MRI (typically < 3 T). So this means there is no major industrial interest beyond NbTi. Further, NbTi is an alloy not very difficult to manufacture - 19th-mid 20th century technology works just fine. Going beyond NbTi, one will enter the zone of half-metal or ceramic, which is harsher for kilometer scale wires. So this means if a more powerful collider is to be built, research facilities need to build their in-house raw material manufacturer. But research facilities often perform poorly in this type of tasks, especially in efficiency and cost-control.

It is fair to say, from the point view of key technology, we are not much better off than the time when ssc was shut down. A key reason ssc was killed is that the project began based on overly bold bet in technology not yet ready. FCC may end up the same way...

As someone who used to work on the technology/engineering side of this issue, I do not feel qualified to get involved in any theoretical discussion. On the other hand, as a well trained applied physicist with considerable amount of interaction with colleagues on the theoretical side, and also as a "drop-out" who is in a more realistic world and can retrospect from a different view of point, I feel qualified to say the following

- When a tax-funded science project comes with a multi-billion dollar price tag and will very likely keep asking for additional funding, the social impact and general public response cannot be neglected. "Tax money got wasted anyway, here or there" type of argument is really weak and may even back-fire. Citing war/defense expenses is not a good one either. From another point of view, barbarians-at-the-door-step is a far more persuasive reason. Sad, but true.

- HEP community as a whole, in its dealing with the general public as well as with the broader scientific community, should act in a more open and humble way. A strong and open sense of entitlement hurts. Do not be the fish that takes all the oxygen in the tank. Looking back at the failure of ssc, opposition from other scientific communities played an important role.

- Not building a next bigger machine really does not mean the termination of HEP research. Of course, it will mean shrinkage of the field to some extent, less people, less money. But to be realistic, scientific research conducted by human is still a social activity down to the bottom, so no forever growth is guaranteed. There are many alternative ways for HEP to continue without a bigger machine.

- HEP and the entire science community need to cautiously weigh the negative impact of a bigger machine failing to deliver meaningful finding ( to be clear, I am not qualified to judge if a HEP finding is scientifically meaningful or not, but I hope everyone agrees that certain types of findings are easier to make sense to layman than others). Big promise and no deliverable may blow HEP and the entire science community much harder than deferring the next big collider to a later time.

“Big promise and no deliverable may blow HEP and the entire science community much harder than deferring the next big collider to a later time.”Yes, absolutely agreed – here about the same in other words.What you said here was also very interesting: “An example commonly cited by HEP community …. successful incubation/creation of the MRI market …. questionable in the 2010-2020 age … So this means if a more powerful collider is to be built, research facilities need to build their in-house raw material manufacturer. But research facilities often perform poorly in this type of tasks, especially in efficiency and cost-control.”Decades ago I used NMR, spectroscopy rather than imaging MRI, for analyzing how proteins fold with a ∿10 T Bruker machine. Industry and collider research inspired each other, but now as you said “there is no major industrial interest beyond NbTi.”Your “A key reason ssc was killed is that the project began based on overly bold bet in technology not yet ready.” suggests, I would say, that we better first invest more money in material science, better understand super conductivity and what Sabine says wait for better reasons from HEP, before we just rush to the next collider and risk a damage to the entire science community with too high expectations in physics beyond the standard model.

"A key reason ssc was killed is that the project began based on overly bold bet in technology not yet ready.”

I don't know who wrote this... Sabine?... but it is not correct. The SSC was shut down for purely political reasons... the mid-term elections with a democratic president, bill Clinton, doing nothing to save a big project in a state which two years earlier had voted against him. SSC was certainly going to face major hurdles, as a project, but the technology issues were not the reasons for its demise.

There's a huge potential, untapped source of revenue available to our government in Washington. That is the flow of dirty money south across the Mexican border from illegal drug sales in the United States. Drugs flow north in vast quantities across that border, while 100 billion dollars flows back south to enrich the cartels. If a barrier of some kind could intercept 20%, 40%, 60%, or whatever, of that cash flow, a rather nice windfall would be in the hands of our government to fund all kinds of nice things. If such a situation were to come to pass, opposition to building a new accelerator, at least on financial grounds, would be considerably mitigated. One could even imagine the SSC project in Texas being reactivated.

This FCC is probably a big science gamble. The phenomenological understanding of what is possible is far more murky than with other big programs. Of course as has been pointed out there are other boondoggles, such as t'Rump's silly wall. The US has also deployed a fighter aircraft, the F-35, that has marginally better performance than the old Soviet SU-22. The F-35 goes for a 120 million dollars a piece, while the SU-22 was produced at less than 1/10th that cost. The US fielded the space shuttle program for 40 years at an enormous cost before eventually giving up on it..The FCC at worst would be in the fine tradition of over budget boondoggles.

Bahle wrote: What it boils down to then is the hope that not building the FCC will funnel the money into other ventures that collectively, have larger benefit . . . I'm probably a cynicist I guess, but I'm not sure about that.

This is a more subtle argument than the "peanuts" argument. I wouldn't say you're a cynic for bringing it up, but even if there's some truth to it, that's not a persuasive argument against the approach Sabine has outlined. Of course there are other scientists besides Sabine who have offered ideas for improvements.

Has anybody considered the negative public-relatins consequences to physics of building a twenty billion dollar machine and having it not find anything? That is what I think physicists should be worrying about.

Of course, if physicists sell it as "We want to build a 20 billion dollar machine that probably will just add a few more decimal points to the properties of the Higgs boson, but maybe it'll find something truly exciting" then there might not be any negative reaction when it doesn't find anything. But do you really think you could convince people to fund a machine with this argument?

I agree that it seems like this should be the argument against, in terms of persuading someone who is inclined to be pro twenty billion dollar machine. I wonder though (cynically) if the time horizon of such a large project is essentially enough to span someone's entire career -- a current grad student could put her kids through college before the public gets wise.

Yes indeed, the damage of another lap of null-results in the wake of high expectations in physics BSM could be significant. I hope the damage would be restricted to particle physicists only and does not spill over to science in general.Your argument should weight in the discussion. The price tag (seen as kind of negative externality) of the damage could be way over $20 B on top of the money spent for just building the next collider.Thus, we better think twice before rushing to the next one.

The crappy nonsense arguments that particle physicists in failed rebuttals to Sabine are already enough of a public relations nightmare. The fact that scientists are using ridiculous economic nonsense arguments and refusing to accoubt for the huge glut of failed predictions at the LHC is already disastrous for the reputation of HEP.

Is anybody here aware of the spin-offs of a large accelerator-based research institute ? - CERN trains hundreds of technical personnel per year in science and technology. After their apointments with CERN they go to industry in the member states and apply what they have learned in an international, collaborative and competitive environment. The benefits for international understandg and spreading of science and technology are hard to measure. - Someone said, MRI stops at 3 Tesla, but forgot to say that this is the safe limit for magnetic field strength from NbTi superconductors cooled with liquid helium. The LHC works now with fields of up to 8 Tesla, only possible with (costly) superfluid helium technology. New superconductors of the NbSn3 type, or High-temperature superconductors would open the door for hgher field MRI, which means better resolution and therefore better diagnostics. - Detector and accelerator technology from particle colliders has entered the field of medicine in proton- and hadron treatment facilities and better X-ray scanners (lower dose to the patient).

Stopping this field and waiting that someine develops, out of the blue, a better accelerator (with better magnets,as I read above) is not working, you need a maotivation to develop these technologies, and you improve with every colider built.

More powerful magnets are in the pipeline. 11T dipoles are being built (40% increase to present LHC-standard), 16 T is the FCC baseline, and 20 T may become possible with high-temperature s.c. I wanted to express that this research will not continue if there is no motivation for it, e.g. a next collider. Don't expect Siemens to spend the money to develop 8T MRI systems, when they can make profit with 3T magnets. The technological breakthrough in these fields comes from publicly funded R&D.The construction of a large collider forces the new technologies to come out of the laboratory-prototype status and to be industrialised. For LHC, 3 European companies deliverd dipole and quadrupole magnets on an industrial scale. The fact of having industrialised the technology makes a transfer in other areas, for example medical technology, simple. I doubt that you could easily transfer the lab-type echnology used to build a one-off 16 T magnet for Bose-Einstein gases or quantum computer with trapped particles easily to medical technology, the cost of industrialisation is too high. In a collider project, this cost is an overhead of the delivery cost and amortised with every exemplar of accelerator megnet delivered. The same example may be repeated for other technologies, I pick magnets because they were advocated above as "not worthwhile improving".

Tell us, just how does the Higgs allow us to observe all kinds of processes of objects that make up our universe?

I'll give you the perspective of someone who, since getting a PhD in physics a half-dozen or so years ago, has been working independently on particle theory from a very different direction (which I won't discuss) than the conventional one. Although most new approaches turn out to be dead ends (that's why we're stuck, right?) I think it's relevant to your question.

First, I think the "real" reason we're stuck is that we've pursued energy (Lagrangian/QFT) and symmetry methods about as far as we can take them. We have the very successful Standard Model, and attempts to extend it often rely on notions of naturalness and larger symmetries -- forms of beauty that you have repeatedly noted "just haven't worked" for several decades. But those notions of beauty are invariably in the context of energy and symmetry methods.

There is no question that energy methods are "battle tested" and predictive in successful QFTs like QED, QCD, and electroweak theory. But because they apply to ensembles, we can get only statistical predictions and tests, which are fine as far as they go. But the success of the SM doesn't imply that a deeper description of Nature isn't possible, one that allows explaining why QFT works so well or even deriving QFT principles from it.

Personally, I believe attempts at BSM theory and even quantum gravity are flawed because they all seem to assume that quantization is fundamental--something to be encoded in the axioms of a fundamental theory--rather than an emergent phenomenon. That is, I believe QM and GR don't work together because they share a common origin which isn't reflected in the postulates of GR or QM. To repeat: this is my perspective and is not widely shared, but it drives much of my research. Sure, not much has been proposed (yet) that explains how quantization emerges, but that doesn't mean it doesn't. Moreover, I expect internal symmetries of particles should be derivable from a deeper theory. Clearly, no theory of emergent quantization or internal symmetries will come from energy methods alone -- they are too blunt an instrument.

This gets to your question. At least in my research, which focuses on why particles have the internal symmetries and other properties they have, the Higgs field plays an absolutely crucial role in the discreteness of the mass spectrum, beyond just "giving mass" to various particles. Empirically knowing the shape of the Higgs potential is of prime importance for determining whether approaches like mine have much hope of offering a path to progress in fundamental physics.

So I'm basically arguing that progress in fundamental physics may require understanding the fundamental origin of elementary properties of particles (spin, charge, mass quantization, ...)--something QFTs can't do--to make real progress. That is, we may need to move from BSM to WSM ("Why the Standard Model"), and precision measurements of the Higgs could play a key role in that.

One general comment first (summarizing also after of your some previous posts). You keep on insisting that there was no advancement in our understanding of the foundations of physics in the last 40 years. First of all, I don’t think it is wise to “put a clock” on something like this and measure how often a new idea comes about. Lamenting that this hasn’t happened in 40 years is “strange” and should make people reflect, ironically reminds me of your issues (which I completely agree with, by the way) with probability distributions, priors and the elephant in the room, the “hierarchy problem”.

What is the probability distribution for big advancements in the foundations of physics? Which one are you using to say that 40 years without advancements is an “unnatural number”? It is ironic but, it is my impression that your argumentations use sometime the very same ideas that you so strenuously fight against…

Having said that, saying that there were no advancements in the last 40 years is naive and wrong, for two reasons:

1) Experimentally, in those years thanks to the collider physics program we have discovered a lot of fundamental particles, most notably the Higgs 7 years ago, the top-quark in the 90s etc. The fact that the theory was so ahed of the experiments is an incredible success of theoretical particle physicists. To me it looks like you don’t give credit to this enough and forget that, before experimental confirmation, a theory remains a potentially wrong theory. So the last big leap in our understanding happened, indeed 7 years ago, not 40. Theory and experiment proceed not always exactly in parallel, but they are both necessary to make “advancements in the foundations of physics”.

2) On the theory side, expecting to have a new revolutionary idea, and also a correct one, every couple of years, well what is this if not naive? History teaches us that our understanding in physics has advanced in two ways. Either someone with a genius outside the ordinary has made a huge leap forward in a little amount of time (simplifying a bit, Einstein with GR), or experiment has guided theory developments step by step (QM). This second possibility requires usually very inexplicable phenomena, which can also give punctual and precise indications in a laboratory on where to change the current theory.Now, even if today a deviation to the predictions of GR or the SM were found, I do not think that finding a 1% deviation in the transverse momentum distribution of the Higgs or in some gravitational wave pattern is gonna tell us much on how to improve the theories quantitatively for real. It might happen, of course, but if the theories have worked so astonishing well till now, how can we imagine that improving the sensitivity a bit or the energy a bit is gonna change anything?

I don’t know of course what is gonna happen, but this is only to say that, but we might be historically in one of those times where actually a new idea is needed, one of those that revolutionize completely our way of looking at things.

So the question we have to ask maybe is, how can we foster this? In one of your answers you ask, quoting someone else, “how does the Higgs allows us to observe all kinds of processes of objects that make up our universe?”.

Well, last time I checked, the Higgs was part of our universe. Has something changed in the meantime? Actually, the Higgs is also the only part that we have seen and that we don't understand (no one has seen dark energy or dark matter, for real). To me, this is enough to say that one of the most promising chances we have to go forward is looking into the only thing that we know is there and that we don't understand, aka the Higgs.

So I'd say, please, let's stop arguing and go see what this Higgs is really made of ;)

I have been abundantly clear, here, in my book, in my lectures and so on, that what I am referring to is that we still use the same mathematical formulation as we did in the 1970s, as with the SM completed and GR in place. And that is even though we have problems (notably QG and dark matter) that we have known of since 80+ years.

Yes, we have measured things after this, but the successful theoretical predictions for new phenomena predate this time. Since the 1970s, all theories that were newly developed were either false or unfalsifiable.

More precisely measuring the properties of the Higgs is all well and fine, but it is not currently a promising avenue to pursue.

As always, you are completely, and at this point what I can only assume is purposefully, misrepresenting collider experiments and their purpose using outrageous claims.

"That a larger particle collider is not currently a good investment is hardly a controversial position."

That is your opinion, and it is in fact a pretty controversial one.

"But the unprecedented social advances have not come to pass, and neither have we since seen major breakthroughs in collider technology. The state of affairs is often summarized in what is known as the “Livingston Plot” that shows the year of construction version energy. You can clearly see that the golden years of particle accelerators ended around 1990."

What is your point, that the log-log relation between energy and time can not stay constant? Obviously it can not, otherwise we will soon be constructing planet-sized accelerators, and obviously colliders will never be used to probe the planck scale directly. At some point collider physics will reach a physical barrier just like transistors, and we will probably stop. So what? If we had followed your golden year argument we would have stopped at the Tevatron, and never observed the Higgs.

"In the plot below I have collected some numbers for existing and former colliders."

In fact it looks like we can improve energy exponentially with cost, so this seems is quite efficient. It also doesn't make much sense to have lepton colliders and a bunch of other things on the same plot as hadron ones.

"There is currently no reason to think a larger particle collider will do anything besides measuring some constants to higher precision."

This is incorrect, it will for sure be able to measure constants (like the self coupling of the Higgs or rare decays) that can probably not be measured at all at the LHC, so it is not just improving some decimal accuracy, but measuring new fundamental constants of nature.

"But this knowledge will tell us little new about the universe and it cannot be used to obtain further knowledge either."

It will tell us what the Higgs sector looks like, which is definitely something new about the universe. If there are any deviations, which is absolutely possible, it would tell us also a lot about how to obtain further knowledge.

"Compare the expenses for CERN’s FCC plans to that of the gravitational wave interferometer LIGO. LIGO’s price tag was well below a billion US$. Still, in 1991, physicists hotly debated whether it was worth the money."

The debate with LIGO was whether the experiment was technically feasible, which is not really under question for the FCC. So the comparison of the two debates is rather meaningless.

"But this was not a situation in which “nothing until 15 orders of magnitude higher” was the most plausible case."

No serious physicist thinks that nothing for 15 orders of magnitude is "the most plausible" scenario. Sure, there is no strong reason to expect that new physics has to show up between O(1) and O(10) TeV, but if the lesson you take from null results at the LHC is that this is "most likely" (i.e. > 50% probability ?) to hold for another 15 orders of magnitude, then you are definitely far outside of the consensus. Who knows, perhaps you are right, but I definitely would not take that bet.

"A particle collider tells you more about particle collisions. We have found the Higgs, all right, but there is nothing you can do with the Higgs now other than studying it closer."

If you follow this kind of argument we might as well have killed off the whole field 50 years ago. Which of course you have the right to think, but a lot of people disagree and see value in measuring and understanding nature at smaller scales, even if it is not of direct practical use.

"That’s why high-precision measurements, like that of the muon g-2 or the electric dipole moment, are an alternative to going to higher energies. Such experiments are far less costly."

These experiments are not "alternatives". They probe very specific things and can not do anything close to the multi-purpose potential of large colliders. Obviously they are very useful and one should do them, but comparing their costs directly makes no sense.

"With that, the standard model is complete and no reason to expect anything more."

That is just your opinion.

"They do have a large number of predictions for new particles within the reach of the next larger collider, but these are really fabricated for no other purpose than to rule them out. You cannot trust them."

Yes, in the absence of meaningful new data, model builders will try to use their skills to come up with interesting or somewhat plausible scenarios that could be probed at new experiments. Obviously most or all of these will be ruled out once data comes in to check. It is the way science works, and every now and then we might get lucky. That does not make them dishonest as you are trying to depict them to your followers.

Note that I agree that there should be an honest debate about the pros and cons of funding new colliders, and that it should not happen by default as a way to "maintain knowledge" or just because collider experiments tend to have good indirect returns in technology and society. But the arguments you provide are biased and incomplete, and if you want your opinions to be taken seriously by the community you are criticizing, then you should at least do the work of reading the actually physics reports on the topic and engage in a meaningful discussion rather than repeating the same high-level clickbaity hot takes every few days.

The standard model is NOT complete: it has zero neutrino masses and since about 15 years we know that this is not the case. So, there is a loophole into some unknown territory: if the neutrino is massive, then where is the right-handed neutrino? Or is it of Majorana type? I am only wondering why CERN didn't pick this up as a major future line of research? The answer seems to be that even on the high-energy physics side there is a 'battle' going on between collider-enthusiasts on one side and neutrino-proponents on the other and the collider-people won.

Long-baseline neutrino experiments are ∼$1B-scale projects that can be carried out by casts of hundreds, not thousands like LHC (of FCC). They are just now big enough to serve as a flagship project for a laboratory as large as CERN.

Long-baseline neutrino experiments are ∼$1B scale projects that can be carried out by casts of hundreds, not thousands like LHC (of FCC). They are just now big enough to serve as a flagship project for a laboratory as large as CERN.

Sabine, nice post (as always) and great job in digging out the NY times article on funding of LIGO. Do you have any such information about funding of Gravity Probe B and AMS? Both these experiments were funded, despite opposition from lots of scientists.

I didn't actually dig it out, someone sent it to me in reaction to the response letters to my Op-Ed. So please don't credit me too much for my investigative skills ;) I know very little about Gravity Probe B and AMS, but maybe someone else does?

The extremely valid arguments made in this blog about the lack of objectivity in current high energy theoretical Physics (lack of objectivity being due to a misguided pursue of beauty or simple detachment from Reality is of secondary relevance what really matter in natural sciences is objectivity) are ironically undermined by posts like this one because the only way to gain more objectivity in our notions about Reality is to gain more and better empirical evidence not less.

The alternative to this will be more (cheap) post-empirical arguments trying to justify ideas, or even books claiming that the dinosaurs were exterminated by a dark matter asteroid.

Doing always had been and always will be harder(and more expensive) than talking.

You fail to take into account that we have seen 40 years of experimental results with lots and lots of data, and that has done nothing to cut down the theory-jungle. Rather the opposite, it has encouraged its growth.

The reason is that all that data only confirmed the already existing theories and did not deliver evidence of new phenomena.

Therefore I say we should pursue a road where we have good chances to find evidence of new effects, not further null-results. Null-results are also results but they are not very useful results if you want to develop a new theory.

We currently have no good reason to think a larger collider will do anything but confirm the Standard Model, hence it is not a promising avenue to pursue. Instead, study closer those cases where we have inconsistencies between experiment and theory, or internal inconsistencies in the theory.

Another important aspect of this to examine is the claim that development of the FCC will create great economic and technical benefits. As an accelerator physicist, I actually think that many of the other accelerator based projects would give more back for the investment. I worked at a synchrotron light source for many years, and found the support on the accelerator side lacking. It was expected that the institutional support would come largely from high energy particle physics. This means that only certain topics and technical developments occur. I don’t want to criticize the amazing accomplishments of particle physics, but its time that other perspectives and goals are seen as important enough to motivate public and institutional support at the same level. Particle accelerators are great, and produce many benefits, but supporting high energy colliders in a disproportionate way does not serve society in my opinion.

"I worked at a synchrotron light source for many years, and found the support on the accelerator side lacking. It was expected that the institutional support would come largely from high energy particle physics."

What??? Utter nonsense. Light sources are everywhere. Europe alone has more than 10. The biggest one, the ESRF, finder like Cern by many countries, is under full refurbishment right now... they are formatting dismantling the storage ring to build a new one, with ultra low emittance. Basically all other existing light sources have plans, and some of them the money already, to do similar upgrades: Swiss light source, Italian, French, British, 2 in the USA... APS and ALS... one in Germany, Petra-4, Russia, China(2 or 3)... Australia, Brazil, Japan (more than one)... and probably more. Light sources are well funded... of course this doesn't mean that there is no need for more, quite the contrary, they are extremely useful to do other type of research. Are you sure you have worked at a light source?...

Hello Roberto,Indeed, I worked at the ESRF and know all that you write here quite well. Wow, "utter nonsense" is a rather strong expression... it doesn't really encourage me to respond.

Its true that these upgrades are underway which I think is a good thing. The point is that there is little understanding of the accelerator side from the scientists (condensed matter physics, biology, geology...) using the synchrotrons. They treat the x-rays mostly like electricity that it is the job of the electric power company to provide and they shouldn't have to think about it too much, though they do need to pay for it.Whereas in high energy colliders there is more of a scientific partnership between the particle physics and the accelerator physics, the same is much less the case in the light sources. This may change with these upgrades, but I still had the sense that most people look to high energy physics for the inspiration and support for the discipline of accelerator science. I don't see building the FCC as having a strong positive impact on the accelerator physics of the light sources, though I could be wrong. This is what I meant by suggesting we examine how useful for technical spin-offs building the FCC would really be.

I have been told that while the decision on the Japanese plan is strictly speaking only due in March, it's pretty clear already they will not go for it.

As I said earlier, if there is nothing new in the LHC run 2 data, I doubt the Chinese will build their collider. It is true of course that such an an investment would bring international reputation, and is worthwhile for training and importing knowledge. But the same can be said about any other large-scale experimental science investment.

The Chinese, in my impression, want to leave a mark in history. If they put their money on a larger collider, chances are they will enter history as the first nation to build a huge particle collider that didn't find anything new. The last thing they want is end up being laughed about, so they won't.

Btw, the Chinese were the first to buy the translation rights to my book.

I don't know enough about how the funding decision would proceed to make any reliable prediction for that, sorry. I can only talk about the scientific aspects, and what I am saying is that if you want to invest in progress in the foundations of physics, then the FCC is presently high cost/little benefit.

Of course if there is something new to find in the 2nd run data that would entirely change the situation.

??? Nonsense... comparing apples of 20 years ago to oranges of tomorrow. How about the costs, and time frames, of the proposed new advanced gravitational wave detectors? How about LISA?... 3 spacecrafts to be sent in space millions of km from Earth by the boondoggle multi-tens billion dollars PER YEAR NASA? How about that, Dr hossenfelder?

Ah, here comes again Roberto Kersevan from the CERN technology department in his tireless efforts to show us the unfathomable depth of his knowledge. Have you finally found the "solid mathematically and logically sound foundations" according to which the FCC should see new fundamental particles? Has it doomed on you yet that there aren't any?

Yes, what about LISA? LISA will look for signals of supermassive black hole mergers and primordial gravitational waves. We have good reasons to think that (a) there is something to find and (b) finding them would help us learn a lot about the early universe and galaxy formation.

"Roberto Kersevan from the CERN technology department in his tireless efforts to show us the unfathomable depth of his knowledge."

Yes!.. that guy who's been designing the FCCs since many years, and could easily correct all the wrong statements you've made so far. Talking about the pretense of having unfathomableble depth in knowledge... you're just talking about yourself, right?.. It's not me the one who knows everything, to the point of writing a book!...

"Costs for LISA are quoted here with 1.3 billion US$."

Sure!... NASA is known to never overblow its budgeted costs!

What's next? The fairy tail?

Correct your false/fake statements about the costs and timing of the FCC, and then we'll discuss again... did you make the "ten years"up yourself? Why?To show that the yearly costs would be "too high"... like 1/10 of what Germany alone spends to "inventize" PV? Get real.

Thanks for clarifying that, doesn't change much in my conclusions.Sabine is comparing apples ton oranges.How could a rational mind compare a device which is orders of magnitude less complicated than an accelerator like the lhc, or FCC?... do you know how a gravitational wave detector is made?... how could one compare a device which basically does only one thing to an accelerator complex capable of doing multi-disciplinary research? How?

Really good points! In my perspective they just want the money... There is no solid theoretical prediction they are trying to search for. They will search in the dark for something they dont know. They have to somehow "save" their careers. Of course this huge amount of money can be used in a better way of course.

"If you think it is only "my opinion" that there is no reason to expect anything more until all the way up at the Planck scale, how about you name us a reason?"

For example, the upper bound on the mass of right handed neutrinos is several orders of magnitude below the Planck scalehttps://arxiv.org/abs/hep-ph/0006358https://arxiv.org/abs/1303.6912

This is not to say that this is best probed at the FCC, but repeating over and over again that the standard model is complete and there is nothing to expect below the Planck scale does not make it truth. In fact it is wrong on both counts: we know the SM is not complete, and there are pretty good reasons to expect new physics will show up below the Planck scale.

Thanks for the reference. I think I misunderstood your earlier comment, sorry about this. You are right that speaking about the Planck scale is sloppy. Depending on which argument you look at (qg/GUT/see-saw) the scale of new physics may be one or two orders of magnitude below the Planck scale.

I don't see, however, how that's relevant to the question of whether we have reasons to think the FCC will see something new.

Roberto, your „arguments“ here remind me of an defensive animal. You better stop that and provide some sound indications for public value that a FCC will deliver. Otherwise I will never support that you see even a penny. And I am saying that not just as a member of society but also as a physicist. I don’t like to see you and many colleagues to risk the relationship between fundamental science and society just because you fear that something in your life will change when you cannot slip from one big collider project into the next one.

Let me say that (without actually agreeing with her on whether the FCC is a bad or good idea), I think Sabine is doing a great service to science.

Let me ask a slightly different question:

Should we lie to the public and funding agencies about what the FCC is likely to find in order to get it built?

I hope that everybody will agree that the answer is no.

And this is where we need things like blog and Sabine's book Lost in Math. Without a pessimist like her to counterweight all the optimistic theorists, we might end up essentially lying, because the physicists arguing for the accelerator would end up citing all the optimistic theorists' unrealistic predictions. Whereas now, hopefully, if anybody builds the FCC, at least they will have realistic expectations for what it will produce.

Let me say that attacking Sabine is not going to help; rather than spending energy time attacking her, you be coming up with good arguments for why we should build the FCC.

Needless to say I entirely agree that FCC enthusiasts, rather than attacking me, should come up with good arguments to spend money on their pet project. It's difficult, of course, because there aren't any good arguments.

Allow me to add, however, that I do not argue against the FCC because I am a pessimist. On the contrary, I think there are better things we could be doing in the foundations of physics than measuring some SM constants to higher precision. If we put our money on the wrong horse, we may not see progress in the field for another 30 years. I don't want that.

I have to a degree been on the fence with this. I can see the argument that probably all we will find is more standard model physics and nothing terribly new. However, there are some possible things that might exist in the 100TeV range. There is some possibility for sphaleron physics with B - L physics and baryon/lepton asymmetry of the universe. Maybe supersymmetry operates with this energy scale and with this instanton physics.

There is a sort of Forrest Gump factor; you never know what is in a box of chocolates until you open it up. So from a purely scientific perspective I can see the argument ”damned the torpedoes, full speed ahead.” Of course there are the caveats with this, and in particular such hyper-programs can impinge on other science, and that is where the real problem is. The 20 billion € cost is not that big a factor in the world over all. Back in 2008 when Lehman Brothers imploded, in the wake of Bear Sterns going under, George Bush looked at the abyss we were heading towards and negotiated with the Federal Reserve to generate several hundred billion dollars. Obama got into office and did the same to the tune of $4trillion, though some of it was TARP that was mostly paid back. This was money literally created out of nothing and within the context of the financial meltdown most “in the know” policy makers had few problems. The alternative was disaster. Those decrying this were borderline miscreants in the so called Tea Party. A science and technology program that would enter this magnitude would be sending astronauts to Mars. Given that $2 trillion in currencies are exchanged daily, these big science programs such as the LHC and FCC are really small potatoes.

As I see it the funding of such large programs needs to be argued within the context of how this will compete with other science, which includes not just physics research but things such as bio-medical or climate or … . The other main issue here seems to be one of public relations, where a big science program that finds little of anything new will appear as a black eye. This needs to be made clear if the FCC were to go forwards; this is a big gamble and one that might not yield much. Yet we can't know unless we actually do the experiments.

I think you are gauging your assessment with the wrong scale. How is the amount of money shuffled around the globe relevant to the question whether a larger collider is a big investment or not? You should compare it to other large experiments in the area (or even in other areas) and you will find that it's way more expensive. I have already given some examples above, but you can do your own Googling and will find that other experiments typically range from 0.5-2 Billion. Colliders really are pretty much the most expensive thing you can do.

To give you another scale to gauge from: I can't get 20k Euro to pay a student for the work they are doing. I hope this helps you understand why I think 20 B is a lot of money.

„Yes!.. that guy who's been designing the FCCs since many years, and could easily correct all the wrong statements you've made so far.“

Why don’t I see you doing that?

It is neither Sabine nor anybody else how is in charge to provide arguments. It‘s you and your colleagues that whant my money. The only people that are in charge to provide convincing arguments are you and CERN.The public does not need to justify why they don’t want to let you waste their money.

CERN would be well advised to replace people like you if they don’t want to ruin their relationship with the public. And with this, their survival.

We are simply making a scientific case/proposal for a new accelerator... actually, a suite of accelerators. The one asking for money is the scientist Sabine, who doesn't want to publish her positions on regular physics journals.. you have to buy her book of Revelations... :-)

The FCC proposal rests on solid footings, in spite of what the blogger, you, or anybody else may claim. The said proposal rests on solid footings not only for what concerns the design of the accelerators, in fact the FCC-ee could be built tomorrow as far as technology is concerned, but also the experiments, including the breath of possible discoveries in the field of particle physics and possibly more. There is a rather comprehensive and thick volume of the CDR which deals with that... if you are a physicist you won't have any problem at all to find a copy and check that what I'm saying is the truth. Go ahead, make my day.

At any rate, the EU GNP is 19.1 trillion dollars/year, i.e. 2.2 billion dollars per hour. Thinking that the EU couldn't fund a scientific project that for every € it spends on it generates much more in the general economy ... in fact most of the money would be spent on materials and services from companies like the one you are employed at, FE-Design... an investment equivalent to 10 hours or so of its GNP.. but in 20 years!... it is mind boggling how myopic one can be!!!

It is also mind boggling to me that you suggest that I would be after YOUR money, when actually the company you work for is owned by a French conglomerate which has been making A LOT of money out of the paychecks of French residents like me (in the form of taxation), thanks to the hefty "public" contracts with the French military and publicly-funded (and often bailed out at the taxpayers' expense) companies like Airbus. So, please!... have the decency not to go into that argument, ok? Later.

I‘ am not employed at FE-Design since nine years. The company does not even exist anymore after it was acquired by Dassault. In my times there, it was just a small company on it’s own. Your research failed totally.

As a member of public I'm genuinely curious. Did any recent, lest say last 40 years, advances in fundamental physics allowed us to do any better or new engineering?

What return of investment do we get or can expect to get? There seems to be some benefit in doing engineering around big scientific projects like data processing etc., but this benefits seem to be tangental. We could very well direct 20 billions more into human Mars exploration, get similar engineering output and on top of that inspire millions of kids to become scientists of the future. Seeing people on Mars would so much more inspiring than discovering Higgs boson.

Am I correct in thinking, and this is genuine question, that theories that can not be even tested with billion dollar budgets and kilometer scale machines will not and can not have any direct impact on everyday person lives?

I'm sure Einstein did not expect that General Theory of Relativity will be used in self-driving cars some 100 years later. But I would think that he would agree, that his theory could have serious engineering implications.

Can String Theory or Super-symmetry proponents say the same?

Also, don't get me wrong. I love physics. I think there is value in exploring physics just for the sake of knowledge, but if this is the only output I can reasonably expect I would like it to be clear.

I don't know if Einstein would have anticipated engineering applications for general relativity. They only exist because of the communications satellite, which was first conceived thirty years after Einstein's theory. Einstein didn't even live to see Sputnik.

Any "daily life" impact of supersymmetry or string theory is likely to come, not from engineering that involves extra dimensions or superparticles, but rather from the application of mathematics pioneered there, to some other field entirely. There are plenty of professional disciplines which now employ calculus; we may end up with a world in which artificial intelligences freely utilize concepts first developed in order to navigate the abstract spaces of unification physics.

„Yes!.. that guy who's been designing the FCCs since many years, and could easily correct all the wrong statements you've made so far.“

I would love to see you start doing this. But I don’t. Especially not with respect to the key issues highlighted e. g. in Sabine‘s book.

The only thing I see is that you put a threat on the relationship between fundamental science and the public. CERN would be well advised so recognize this since this is also a threat to their long-term opportunities for funding. By doing so, you are neither helpful for CERN nor for fundamental science in general.

Again: I am (and nobody else from the public) not supposed to explain to you why a FCC might not be worth the price. It’s you who is in charge to explain what you will achive for that funding. Regarding my personal view on this I can tell you, you are not doing well at all.

For the sake of saving time, allow me to caricature the argument on the other side by quoting the ever-reasonable Phillip Helbig:

"In the grand scheme of things, the amount of money is peanuts. Probably more is spent on tattoos and piercings. It is silly to argue against a project because it sounds expensive when one quotes the price tag being borne by dozens of countries over a few decades."

Sabine wrote: Now, factor in the unclear discovery potential for the next larger collider.

Phillip has an answer to that point too:

"I don't see the lack of expectation as a reason not to build it."

As far as I know, I'm the only person who offered a serious rebuttal to Phillip's "peanuts" argument, but he didn't respond.

Sorry, I was busy with real work. :-)

Seriously, I think that one needs to distinguish three arguments against building a new, expensive collider (or something else with a high price tag without a promise of something interesting). First, the price itself is not an issue as long as it is peanuts. On such grounds, one could object to something which, say, costs every person on Earth one-half of their income, but not something which is negligible, even to each and every individual person. So, the price tag itself is a straw-man argument. Second, one could ask what choices one should make, given a limited budget for research. That is a valid point. Of course people will disagree, but a discussion of this point makes sense. Third, there is the argument "one shouldn't build it because we don't expect to find anything interesting", which flies in the face of the way science should be done. In itself, this is not only a bad, but also a dangerous argument. At best, one could use it as an auxiliary argument to support point 2.

If you think one step further you'll finally get there. The budget for research is limited, you invest in the most promising experiments, if you have no reason to expect any breakthrough that's not promising. There are better ways to invest the money.

The haunting comment on this thread is from Mr. Tysannder above. He is following Sabine's general admonition to work outside the fashionable stream of theory, but contrary to her assumption, thinks he could use the FCC's investigation of the details of the Higgs potential to advance his work. Others may be lurking out there. Are we really sure that attaining a detailed knowledge of the first spin-zero particle ever observed, comparable to the detail known about other fundamental particles, isn't important?

@PascalI'm not on the defensive. My job is not in danger just because a person who has not even ever seen an accelerator writes a magic book against accelerators.I don't know quantum gravity, the field of expertise of Dr. Sabine hossenfelder, but I don't go around spewing nonsense about this or that project in that field of research just because "I don't like it". I am back simply passionate in my fight against bullshitters.Cheers.

You came to this blog "spewing nonsense" about BSM pheno, a field that is my expertise, not yours. My "magic book" says nothing about particle accelerators. It documents that your community has a problem. It is great to have you here to prove my point.

Roberto, and still I don‘t see you easily correct the statements or deliver any valuable argument for why your promises for a bigger collider should be true for the FCC.

You say just „bullshitters“ which is noting more that an insult targetet on human beings and not on what they do.

Aren’t you aware how defensive you actually are? It reads like a profound struggle with affect regulation.

Aren’t you aware that you just deliver more evidence for the claims from Sabines book by acting like this? You are helping to make her case by being that angry in a publicly accessible forum - and by not providing convincing arguments for valuable research outcome of an FCC.

The document you refer to lays out what the FCC would be able to do. It does not contain any argument for why that is the best way we can currently invest money if what we want to see is progress in the foundations of physics, which, I hope, is what we all want.

"It does not contain any argument for why that is the best way we can currently invest money if what we want to see is progress in the foundations of physics, which, I hope, is what we all want."

Another astonishingly bullshitting argument from Dr. Hossenfelder! Cern, and the eurocircol collaboration... which is tens of other laboratories and academic institutions (this little"detail" goes always unnoticed in your comments, how come Sabine?) are supposed to do their job of making a study and proposing it to the relevant bodies... it is only up to the latter to evaluate and balance the pros and cons of each of them within the total budget allowable by the present financial situation. In fact, there's a very long list of OTHER proposals in front of the ESPP, isn't it Sabine?... or is it only FCC on the table? The committee will make its independent evaluation and make its recommendations. After that any eventual financing will have to be agreed to by the ministers of research of the member countries of Cern (if Cern ultimately "wins" anything)... a long process... very different from the outlandish picture you're trying to portrait... i.e. the greedy, money-hungry, incompetent physicists at Cern who fill their pockets at leisure. Try harder, Sabine.

Thank you once again for telling me things I already know. As I have said many times very clearly, decisions about what proposals to fund and not to fund are multi-layered, depend on many parties, and usually involve a lot of politics. Those are factors I have nothing to say about, hence I don't. I am here simply to inform people about the scientific promise. (Or absence thereof, as it were.)

I have never heard of Roberto Kersevan but he has been identified as having some kind of role in the construction and operation of particle accelerators.

Sabine and others have cast doubts on the cost/effectiveness of high priced future accelerators.

Roberto is clearly alarmed at what the expression of these doubts may do to the prospects of securing funding. I suppose that is a natural human emotional reaction to a perceived threat, similar in its way to a trade union reaction to announced job cuts. Frustration, alarm, even anger are not unexpected.

And Roberto has made his anger abundantly clear. I think we have all picked up on that by now. More interestingly, when he is challenged to back away from that anger and argue his case point by point (I haven't counted but it feels like Sabine has asked him a dozen times now to list some examples of how the FCC will reveal the nature of the cosmos), every time he replies with...more anger.

Literally, the only thing that Roberto has contributed is anger, personal insults, sneers, sarcasm and snide remarks. This is very strange. I'm not a scientist, I'm an IT civil servant. If I want my organisation to acquire a piece of software, even something that costs just a few hundreds of pounds, I am obliged to provide a business case, including cost/benefits, pros and cons and alternatives. It comes with the territory of spending other people's money.

Why does Roberto feel his line of work should be immune from this? If he were spending £20 billion from his own pocket, fair enough. But he's not. He wants my money, my partner's money, my neighbour's money etc etc. Why should we let him have it? Does it not occur to him that it's not his money by right? He needs the taxpayer's support. Shouting insults at Sabine on her own blog is a very poor business case. He has been asked for some simple justifications and to date has not even attempted to provide anything.

At the heart of this debate is a simple thing: science funding for fundamental research comes from public money. Don't treat the taxpayer like a gravy train, make your case: rationally, sensibly, convincingly and truthfully. Don't act like a spoilt child who can't get their own way. The future credibility of scientists is at stake. I'm a science fanboy, always have been. My experience of my peers is mostly the opposite. The general public don't care about the foundations of physics. My three sisters wouldn't have a clue what the phrase means and even if they did, they certainly wouldn't want £1 of their taxation spent on it. I suspect their feelings are broadly shared outside our little bubble. It seems a near miracle to me that any public money is allocated to the frontier projects. Us science buffs have every reason to be grateful for that miracle. It won't help continue to secure that funding in future if scientists behave badly and undermine the credibility of their profession. My advice to Roberto is to grow up and start acting like an adult - for the long term sake of the whole of science.

"Roberto is clearly alarmed at what the expression of these doubts may do to the prospects of securing funding."

Who? Me? Worried about future funding? Not at all. I'm simply, as I said, against bullshiting and fake news. I'm annoyed by those who have not even put a foot on an accelerator's tunnel but claim to know everything about them!

I am deeply concerned about the sorry state of science when a soi-disant theoretical physicist insults hundreds of scientists, engineers, students, postdocs, etc.. who have been devoting housands of hours of their time, in addition to their daily activities and duties, saying that they are incompetent, they do it for the money,etc... That's what alarms me, yeah...

"Why does Roberto feel his line of work should be immune from this? If he were spending £20 billion from his own pocket, fair enough."

Straw-man argument! Clap! Clap! Clap!

Strickly speaking, for the record... the 20 billions would come out of the pockets of 600+ MILLION EU citizens (plus some extra little countries like India, China, USA, Russia under the form of in-kind contributions)... in 20 or more years.

And... by the way, if you are really interested into money... during the 21 years I've spent in France, I've pulled out of my pockets much more than what would eventually come into them with the FCC ... which is certainly going to be the case since I'll be retired in 6 years or so, while FCC would take decades to get built and operated.

Guys: this obsession of yours with the money issue underlines the very low level of your comments... but if you want to make fools of yourselves go on, keep on doing it... :-)

"Shouting insults at Sabine on her own blog is a very poor business case."

Actually, of you'd read sabine's comments and blog texts carefully you'd realize that I'm on the receiving end of her insults!... she has called me and my colleagues to be money hungry, incompetent, idiots, etc... Don't make me waste more time with you by making a long list of her verbal abuse of many posters on this blog. The fact that it is her blog is inconsequential, because it b is a public blog, as you say, and SHE's being defaming the work of hundreds of people, many off whom are her peers!... Had she done it in her book of Revelations I couldn't care less... or do you think I would be dumb enough to throw away 30 Euros?... the equivalent of 20 years of lavish per-capita funding of the FCC??? :-)

The document you refer to lays out what the FCC would be able to do. It does not contain any argument for why that is the best way we can currently invest money if what we want to see is progress in the foundations of physics, which, I hope, is what we all want.

@sabine""she has called me and my colleagues to be money hungry, incompetent, idiots"

I did not. Stop fabricating things I did not say."

Yes you did! Search for idiot in this thread, and go back to the other thread on the 71" video "full of lies". Demeaning words all the time. I understand that it is a strategic choice, to boost your book, but don't deny it... you did it.

"Why do you think it is appropriate to tell a bunch of lies to politicians?"

... when no lies were proffered?

How about this? Compliments?

"Of course the physicists watching this see nothing wrong with this. Because they know it's bullshit. And they have gotten used to this bullshit, so they think it's just business as usual. The moral corruption that has happened here is remarkable. "

They know it is bullshit. They are morally corrupted. Business as usual, to them.

But no, you are not demeaning:

"demeaning

adjectivecausing someone to lose their dignity and the respect of others."

You accused me of calling you and your colleagues "money hungry, incompetent, idiots". I did not. Unsurprisingly, you have not been able to produce evidence I said what I didn't say.

You told my readers in an earlier post that the FCC would "study and discover the origin of the universe" and that there are "solid mathematically and logically sound foundations" that it would see physics beyond the standard model.

You are either deliberately lying or you don't have a clue what you are talking about. I see no need to be polite about this.

"[...] the scale of new physics may be one or two orders of magnitude below the Planck scale."

In this case the limit is more like 4 orders of magnitude below the Planck scale. Obviously it could just as well be at 10 TeV too, we have no idea.

"I don't see, however, how that's relevant to the question of whether we have reasons to think the FCC will see something new. "

I just can not understand your reasoning that there has to be a guarantee that the FCC will see something for it to be worth building. It simply does not make any sense to me, it is just not how science works or has ever worked. It has very rarely happened history that experiments have come with guarantees of seeing amazing new things and if this was the condition to build anything we would be doing one large scale experiment every few centuries. The essence of the arguments you are using could be applied to almost anything: AMS and studying cosmic rays, LISA and exploring gravity waves, even the human brain or genome projects. If there was a simple and cheap alternative to collider physics to probe higher energies in a systematic way, then sure I would be all for it, but there isn't, and there is no other way to probe the Higgs sector either, which is currently almost completely unexplored. I don't deny that particle physics is in a rather tough spot: our understanding of the universe might not improve much until we have more data, in 20-30 years, and there is indeed a possibility that we won't see new phenomena even at higher energies. It is just the way things are, and there are no shortcuts around it. But it is way way too early to give up.

"In this case the limit is more like 4 orders of magnitude below the Planck scale. Obviously it could just as well be at 10 TeV too, we have no idea."

Look up "slippery slope".

"I just can not understand your reasoning that there has to be a guarantee that the FCC will see something for it to be worth building."

That's not my reasoning. To begin with measurement results are never guaranteed until you make the measurement, otherwise we wouldn't have to make the measurement. What I have said is that particle colliders are extremely expensive and yet we have better reasons that something is to see with other experiments, so we should do those other experiments first. A new particle collider currently is at high cost low benefit. That does not mean it has no benefit.

To put it differently: If particle physicists want an exceptionally large amount of money, I expect exceptionally good reasons why we should give them the money. But there aren't any good reasons.

LISA: I already said this before, huge discovery potential and still at lower cost than a larger collider. If anything that's an argument against building the collider because it shows you can do more interesting things with such amounts of money.

Human brain project: Yeah, I'm not a fan of that, but also not an expert so not qualified to comment.

Human genome: Was well motivated, I'd say, but turned out to be not as relevant as anticipated. Personally I think it's because we haven't understood what to do with the data. In any case, again, I'm not really qualified to judge and not sure why you even bring it up.

So, for you LISA has a high probability to discover something impressive. Can you explain to us according to what probability distribution you make this claim?

And anyway, LISA is about relatively well known physics, not about never-observed particles. It compares more to studying the Higgs in detail than to look for BSM physics.If it's fine to put money to understand better gravitational ways, why not put it to understand better the Higgs?

LISA has a large discovery potential because we know gravitational waves exist and we know supermassive black holes exist. The same cannot be said about supersymmetric particles or extra dimensions.

I already told you above, if you want you can convert my argument into a probabilistic evaluation, but I think it's an overkill.

Regarding the Higgs, I also already said this above. Gravitational waves are good for something. You can use them to obtain information about something else. You can do something with that. What will you do with the Higgs self-coupling?

"LISA has a large discovery potential because we know gravitational waves exist and we know supermassive black holes exist. The same cannot be said about supersymmetric particles or extra dimensions."

You can easily turn this argument upside-down: LISA will study known stuff that collides and produces known waves. It will produce a lot of knowledge about things that we have observed already. Nothing particularly fundamental.Instead, exploring new energy regions never observed before could, in principle, reveal really new physics.

As I said, LISA should rather be compared to a Higgs factory. You know that, that's why you change strategy and now say that studying gravitational waves is "useful". For whom? For what? Not for the general public of course.

LISA will probe a wavelength regime we have not previously measured. It is useful because these gravitational waves carry information about galactic cores and maybe also the early universe which we cannot obtain in other ways. This information in return is important input for our theories about structure formation and the universe's matter/energy budget, which feeds into our fundamental understanding of the laws of nature.

You are right that there is no particular reason to expect this experiment will discover new physics, but it has good motivations regardless by helping us to reconstruct how the universe came to be the way it is.

In any case, if you want to argue that LISA should be defunded, I suggest you take that conversation elsewhere. I am not interested in becoming the world's go-to place to discuss proposed physics experiments.

Now I am just confused. The cost of the AMS-02 experiment is close to 2b$, and this is peanuts? But the 10b$ of the FCC is an outrageously high amount and requires guarantees of finding new physics? What is your limit, 3b$, 4b$, 5b$? How does this line of reasoning make sense?

"What I have said is that particle colliders are extremely expensive and yet we have better reasons that something is to see with other experiments, so we should do those other experiments first."

How do you know that those other experiments have better chances of seeing something? What probabilities do you give to these events that this is such a clear cut case to you? Why is there a better chance of finding new physics in some table top experiment than in looking for deviations in coupling constants of the Higgs?

Sorry about AMS. You are right, I must have confused this with some other experiment. So, yeah, that seems a lot of money. But I don't understand what your misgivings about AMS have to do with the FCC. You need an argument for the FCC, not against some already-funded experiment.

If you look at the history of science breakthroughs came from resolving inconsistencies, either between theory and experiment or internal consistencies. In hep we presently have neither. We have those in other areas. Currently that's eg dark matter (experiment-theory tension) or quantum foundations, quantum gravity.

I don't know why you think I have argued in favor of table-top experiments. It just happens that current experiments in quantum foundations, quantum gravity are not large-scale experiments.

I don't have a probability, but if you wanted, you could do some Bayesian evaluation by looking at historical breakthroughs and extrapolating to the future. But really I think that's an overkill. Let me put it differently: I have good arguments for why we should do something else. You have no argument for why we should build a larger collider instead.

The FCC-ee and FCC-pp will explore the structure of matter in such detail never investigated before. The FCC-ee will be able to make measurements of Higgs interactions and other processes with much higher precision than currently possible. With an order of magnitude more energy than the LHC the FCC-pp will probe 10 times smaller scales. The LHC-pp probes an energy range from which currently only about 15% has been probed. The conceptual design report of the FCC shows it is technically and financially possible to build both colliders.

You seem to dislike predictions for what lies beyond the LHC and use that as an argument not to build the FCC, since according to you there apparently exists no firm predictions of what new things may arise. That is irrelevant. The relevant thing is that there are still many important open questions about particle physics and the (early) universe. Some of these questions might be answered by the FCC.

Science is about exploring the unknown. We do the experiment and see what is out there. The only realistic way of going forward in understanding the behavior of matter is by building a collider that probes higher energies and thus probes smaller scales. An order of magnitude higher in energy is a very logical next step, since this currently technically and financially feasible (There are individuals around on this planet who could fund this whole endeavor privately if they wish). We can only be very thankful to the people behind the FCC that they are trying to push for this in order to increase the knowledge humanity.

To me your efforts against the FCC seem to be very negative. As an ex-member of the Frankfurt institute you are associated with I am quite shocked about your writings and I hope you will turn a page and will instead bring something positive to physics and society.

Yes, that is all well and fine, but there are many ways to explore the unknown and there are many frontiers we could be pushing where we can measure something to higher precision. You can make this argument about literally any other experiment under consideration.

The FCC will cost an exceptional amount of money, so I expect an exceptionally good reason to spend that money. There is no such reason. Indeed, there are good reasons to spend money on other experiments instead.

About your complaint that I am not "bringing something positive":

Fact is, in the foundations of physics we have seen null-results for 40 years. This has gotten the field stuck. Chances are if we put our money on a larger collider we will wait 30 years to get more null-results.

Null-results are also results but if you want to make progress in theory-development they are not very useful results. If you have such a long series of null-results you should start wondering if maybe you are doing the wrong types of experiments.

It is about time that people in the foundations of physics sit together and think about what's the best way to make progress. Throwing money at the problem is evidently not a good strategy. It hasn't worked for decades. Time to wake up.

The reason I am writing here (and elsewhere) is that, in contrast to most other people in the field, I do *not* think that measuring some SM constants to higher precision is the best we can do. So who is being negative here?

„[...] since according to you there apparently exists no firm predictions of what new things may arise. That is irrelevant. The relevant thing is that there are still many important open questions about particle physics and the (early) universe. Some of these questions might be answered by the FCC.“

What are these „firm predictions“ you seem to know? For me that is very relevant if you want my money. Everybody can come up with a plan to build some experimental apparatus and say „give me your money for it, I am going to explore the unknown“.

Which ones are these important open questions that an FCC „might“ answer? I really interested to learn that and what assumptions you have to put into place in a theory (which one?) to bring them into the 100TeV range so that they would be measurable with the FCC. And I would kindly but surely require you to come up with other arguments as just those you used in the past to claim discoveries with the LHC e.g. SUSY particles. To suggest a starting point, I would love to learn about why you expect chances for new discoveries in the range 14-100TeV - and not e.g. 10 or 15 orders of magnitude higher?

I am sadly missing a honest and carefully conducted self-reflection and assessment in the community of how it could happen that there is nothing important new since decades although we spent so much money and time into it. This puts a threat on the relationship between fundamental science (sadly: in general) and the public.

"Particle physicists have not been able to come up with any reliable predictions for new effects for decades. The prediction of the Higgs-boson was the last good prediction they had. With that, the standard model is complete and we have no reason to expect anything more, not until energies 15 orders of magnitude higher."

If I understand correctly, you are talking about the expectation of finding new physics at the Planck scale. This expectation is based on the assumption that the relevant dimensionless coupling constants should naturally be of the order of 1. So it seems to me that your expectations are based on naturalness.

No, it's not a naturalness argument, it's an argument from consistency. Perturbatively quantized GR is not renormalizable and it breaks down at the Planck scale. You simply cannot calculate things in the UV with this theory. It's a situation comparable to that of the Fermi-theory beyond the W-mass. It just doesn't work. We know there must be a solution.

The situation with naturalness arguments is entirely different. There is nothing wrong with the standard model being unnatural. It's renormalizable. You can calculate anything with it as you wish.

This is a really important point. If you have further questions please let me know and I'll be happy to provide references.

Non renormalizability means that an infinite number of counter terms will show up in the Lagrangian. The coupling constants of these counter terms are dimensionless once we absorb their scale using the Planck scale.

You can except these counter term to only show up above Planck energy, only if you assume that all the coupling constants are less than 1.

In the case of the Fermi interaction all the related coupling constants depend on higher powers of the electo-weak coupling constants and therefore they are indeed less than 1.

The coupling constant *is* the Planck mass. Of course if you write down powers of the Planck mass in front of the terms then any further constants will be dimensionless. The reason the theory is non-renormalizable is that the coupling constant has dimension, hence the terms need different powers of the Planck mass to make the coefficients dimensionless and divergences can not be cured by one (or any finite number of) counter terms. I suspect you know all that, I write this just to avoid misunderstandings.

Having said this, of course you can conjecture that quantum gravitational effects become relevant at lower energy scales. Scenarios with extra dimensions are an explicit example of this. (Though adding dimensions doesn't exactly help with the renormalizability.) But really this isn't the point. The point is that the EFT tells you that there is an *upper* limit where new physics must appear *at the latest*.

"The point is that the EFT tells you that there is an *upper* limit where new physics must appear *at the latest*."

This is not a hard upper limit. It is only so if you assume that the the coupling constants for the counter terms are of the order of 1. In the case of the Fermi interaction, it turned out that all the G_F squared terms are suppressed by a factor of g^2 (the electro-weak coupling). Therefore, you could in princple use the Fermi model to describe experiments at an order of magnitude higher energies than the Fermi energy (~246 GeV). Of course nobody does it, because there are many other particles that show up below this energy that make that calculation meaningless.

In the case of gravity, the Planck mass (m_P) is the coupling constant for the R term. For the R^2 counterterms, the coupling constants are some dimensionless constants multiplied by m_P squared. Since we have no idea how to determine these constants, we cannot make any prediction about what the energies at which these terms would become experimentaly relevant.

You are confusing two different things. The one is the breakdown of an EFT. The other is the naturalness of that EFT. Those are not the same things. Naturalness is a property of a QFT (effective or not). It's not a statement about the validity of the effective limit.

It occurred to me that we seem to have another communication problem besides you using the word "naturalness" in a way that does not agree with the currently used definition. Please correct me if I am wrong but I think when you speak of the breakdown of the EFT you are referring to something different than I.

I am referring very specifically to the breakdown of the EFT that we do have, that is perturbatively quantized gravity. In that you by assumption neglect all higher order contributions with coefficients that you do not know. What I am saying is that this theory simply stops making sense at the Planck scale, and you can calculate pretty exactly when (can dig out reference if you want). Saying that there are also an infinite number of terms with coefficients that we don't know doesn't improve the situation.

I think this is a well-defined and rather pragmatic problem. We need a theory that tells us what is going on and don't have one. At the Planck scale at the latest we will know more because the theory that we currently have just stops working.

What you seem to be saying instead is that if you write down an expansion with an infinite number of unknown coefficients then you cannot tell at what point it stops converging. That is correct, of course, but merely saying "maybe it converges" helps you nothing to actually calculate what is going on.

I think that I understand our confusion. I am guessing that you are referring to the fact that perturbatively quantized GR is strongly coupled at Planck energies, and therefore the perturbative expansion breaks down.

This has nothing to do with GR being non-renormalizable. QED is normalizable, and still its pertubartive expansion breaks down at the Landau pole.

I am talking about the fact that once you add the R term to your Lagrangian, the R^2 term also shows up (among infinitely many other counter terms that show up). It is natural to assume that the effects of this term would show up at the Planck scale. If you avoid naturalness, you can not make any assumptions on when it would show up.

That you do not know when those terms become relevant does not help you make predictions is what I am saying.

With QED you could say it's a problem of doing the calculation, you already have a UV-complete theory. For quantum gravity we don't even have the theory.

Think of Asymptotically Safe Gravity. It solves the problem by telling you what the theory is (leaving aside for a moment that ASG has its own problems). So now you can make calculations. My point is merely that the lacking UV-completion is an actual problem that requires a solution, in contrast to naturalness problems which do not require a solution. (In ASG the SM is still unnatural.)

"That you do not know when those terms become relevant does not help you make predictions is what I am saying."

That is also what I am saying. Neither of us can make any prediction about what the next collider will find. Personally, I am very curious to find out, even if it might be a null result.

Regarding QED. It is not a UV-complete theory, since it has a Landua pole. A UV-complete theory should be asymptotically free or flow to a stable fix point.

QCD, for example, is UV-complete, but you cannot make perturbative calculations at low energies because it is strongly coupled. That is why we have lattice QCD.

You can make calculations in QG as long as you are in the perturbative regime, it is an effective theory. What you cannot do is calculate the couplings of the counter terms. You could find these out from experiment, assuming they show up in the perturbative regime.

I am not very familiar with ASG. One thing that I don't know is what they do with all the counter terms. Do they just set them all to zero by hand?

You are right about QED of course, I meant renormalizable, not UV complete, sorry.

I'm not entirely sure how to translate the ASG calculation into the language of the perturbative expansion because they use a different expansion so the (running) couplings they deal with may not be the same as the ones you have in mind.

In any case, no they don't just set those to zero, that would defeat the purpose. Of course they cannot calculate the running of infinitely constants, so they select finitely many that they hope capture they main behavior and then study what adding further term changes about the situation.

Let me just quote the current status from a recent paper by Astrid Eichhorn:

"In practice one cannot work with the infinite sum... and instead truncates, i.e., chooses a subspace of theory space that should contain the relevant operators. Accounting for deviations of the critical exponents from the canonical mass dimension, one expects a set with d_g¯i ≥ d_crit to contain all relevant couplings. The value of d_crit can be tested in larger truncations by checking whether couplings with d_g¯i < d_{g¯i crit} are in fact irrelevant."

You are the one that brought up ASG. In any case, it seems that in ASG the counter terms are not set to zero. Instead, it is assumed that a fixed-point exists and that the counter terms would flow to that fixed-point.

I think that we both agree that it is wrong to assume that nature would behave according to our plans, whether it is naturalness or a fixed-point. What I am claiming is that you are also inflicting your own bias when you predict that the FCC will not find any new BSM. We just don't know and we cannot really calculate probabilities for such an event.

I mentioned ASG as an example for a solution to the problem to explain that what I am talking about is an actual problem (the inability to calculate what happens) and not a philosophical problem (like naturalness).

I did not say, not here and not elsewhere, that I can calculate the probability of finding quantum gravity at the FCC using perturbative quantum gravity. That's nonsense and I have no idea where you took that from.

I am saying there is no reason to think that we should see physics beyond the standard model at the FCC and particle physicists should state this clearly rather than raising false impressions.

"But I don't understand what your misgivings about AMS have to do with the FCC."

You are not understanding me, I have absolutely no problem with AMS. In fact I listened to a talk from Samuel Ting last year and was awestruck by the quality of their results. But you can make exactly the same arguments against AMS as you are making against the FCC: "they are just going to measure the power law of cosmic rays to better precision, nothing to see there!". So perhaps you are just against all forms of big science?

"If you look at the history of science breakthroughs came from resolving inconsistencies, either between theory and experiment or internal consistencies."

This is just not true, there are plenty of cases where breakthroughs came from unexpected places. The discovery of the CMB, proton, X-ray and radioactivity come to mind.

So you want, based on your omniscient science vision, redirect all funding from particle physics to other fields because they are "more promising". Maybe you can throw some machine learning and neuroscience in your mix of suggestions, I hear that's pretty promising as well. Now that I think of it, perhaps we should redirect all of physics funding to those fields, what has physics done for us recently anyway?

"I don't have a probability, but if you wanted, you could do some Bayesian evaluation by looking at historical breakthroughs and extrapolating to the future. But really I think that's an overkill."

It would not just be overkill, it would be pointless because those extrapolations would be garbage and sure to be proven wrong in the long term. But I was trying to get you to admit that you are making implicit extrapolations to make your case, the fact that you can't even answer these questions quantitatively makes your crusade even more misguided in my opinion.

No, I am not against "all forms of big science." That's a straw-man argument.

I am happy to hear you like AMS. I still have no idea what this has to do with anything.

"This is just not true, there are plenty of cases where breakthroughs came from unexpected places."

Indeed, for most of the time in the history of science breakthroughs were experiment-led. You found evidence of new phenomena, then you developed new theories for it.

As a research area matures, experiments to probe new ground become more costly and take up more resources. "Just look" is no longer an option. We have to be careful to select what are the most promising experiments to make.

That's why I am saying we would be well-advised to do experiments where we have reason to think we will find evidence of new phenomena rather than more null-results.

That is, focus on studying cases where we already have discrepancies between theory and experiment. Or focus on cases where you have predictions based on the resolution of inconsistencies. This is what has historically worked. There isn't any such case for a larger collider at the moment.

"But I was trying to get you to admit that you are making implicit extrapolations to make your case..."

I am making very explicit extrapolations from the past to the future. We have seen 40 years of null-results listening to people like you. According to my extrapolation, if we continue listening to people like you we will see more null-results.

We've seen also 30 years of null-results in dark matter direct detection, and so far the answer has been "We need bigger and better (and more expensive) detectors!"You seem to prefer DM over BSM: when should we stop designing and building huge DM experiments?

That is entirely correct. If you think I am in favor of building bigger and better dark matter detectors, you got it badly wrong. Indeed, this is another avenue where physicists have failed to learn from null-results. I have no idea what makes you think I endorse upgrading these detectors.

On the risk that you seem to think my references to dark matter refer to direct detection experiments for specific dark matter particles, let me be clear that this is most definitely not what I say. I say focus in on those cases where you have evidence already. Better gravitational lensing data, better redshift-resolution, better sky-coverage, and so on.

If we have sufficiently many experimental constraints we may be able to figure out what particle it is, if it is a particle. Then we can think about what experiment to make to detect it directly.

"No, I am not against "all forms of big science." That's a straw-man argument. I am happy to hear you like AMS. I still have no idea what this has to do with anything."

My point was that your arguments can be made just the same against funding any other large experiment that have no "fantastic" promises (i.e. most of them). You still haven't told me why this is not the case, you just say that it is a straw-man argument.

"That's why I am saying we would be well-advised to do experiments where we have reason to think we will find evidence of new phenomena rather than more null-results."

Measurements of the Higgs are not "null-results", they add valuable data points to our encyclopedia of the universe. There is also no good reason to expect perfect agreement with the SM in the Higgs sector, we have never looked there and the SM Higgs is a very simplistic theory that could well turn out to be something completely different once we study it more carefully.

"That is, focus on studying cases where we already have discrepancies between theory and experiment. Or focus on cases where you have predictions based on the resolution of inconsistencies. This is what has historically worked. There isn't any such case for a larger collider at the moment."

There are plenty of inconsistencies between data and theory at the LHC, just not ones that you care about.

"I am making very explicit extrapolations from the past to the future. We have seen 40 years of null-results listening to people like you. According to my extrapolation, if we continue listening to people like you we will see more null-results."

Yes this kind of extrapolation based on small numbers always works great, this is certainly a very strong basis to redirect billions of funding from one field to others! And 40 years of null results because of me is pretty impressive, given that the Higgs was discovered in 2012 and I have been in HEP for 6 years!

"My point was that your arguments can be made just the same against funding any other large experiment that have no "fantastic" promises (i.e. most of them)."

I certainly never asked for "fantastic promises". Stop fabricating things I never said.

To begin with what you expect of an experiment depends very much of the area of research. Your muddling in biomedicine with the foundations of physics makes no sense whatsoever. You cannot compare the motivations for experiments in those area.

I already named above several large-scale experiments that I think have very good motivations, LIGO, SKA, LISA, to name a few. The LHC too had a very good motivation. Your accusation that I am supposedly against all large-scale science experiments is wrong.

It is also wrong that my argument could be made against all large-scale science experiments. The LHC and its predecessors are the best counter-examples. They all had good motivations.

My point is there is now no good motivation to build yet another bigger machine.

"And 40 years of null results because of me is pretty impressive, given that the Higgs was discovered in 2012 and I have been in HEP for 6 years!"

You are not listening. I am speaking about null-results when it comes to the development of theories that go beyond the standard model. The prediction of the Higgs goes back to the mid 1960s as I am sure you know. It is a null-result for what the search for BSM physics is concerned.

Yeah, sure, as I said several times, it's all well and fine to study the Higgs-sector. Certainly not uninteresting. How is that worth investing $20 billion, that is the question you have to answer.

"To begin with what you expect of an experiment depends very much of the area of research. Your muddling in biomedicine with the foundations of physics makes no sense whatsoever. You cannot compare the motivations for experiments in those area."

I was giving examples of what I consider rather successful or promising experiments where your same logic can be applied. I still have not heard from you why AMS was a good investment but not a larger collider.

"The LHC too had a very good motivation."

From your NYT piece: "Ten years in, the Large Hadron Collider has failed to deliver the exciting discoveries that scientists promised.". Was it a good investment then or did it fail? Do you not see how what you are saying is even more misleading to the public than the BSM predictions that failed to materialize?

"It is a null-result for what the search for BSM physics is concerned. Yeah, sure, as I said several times, it's all well and fine to study the Higgs-sector. Certainly not uninteresting. How is that worth investing $20 billion, that is the question you have to answer."

Collider experiments have never been only about hacking off search space of BSM models. That you see it through that prism is your prerogative as an ex-BSM theorist, but it does not make it any less incomplete a view. Going directly to the media with your grievances is in my opinion harmful to science as whole, not because you are "telling the public the truth" but because you are distorting the debate to fit your narrative.

Also, your arguments for funding seem to boil down to the fact that you know better than funding agencies what is worthwhile and we should all just call you up for your gut feeling on whether something is "promising" rather than bother with 1000+ page reports on the physics case of an experiment.

"I still have not heard from you why AMS was a good investment but not a larger collider."

I didn't say it was. You did. I haven't said anything about whether or not it was a good investment and frankly I am not interested in discussing the matter. If you want to post-evaluate funding of your favorite experiments already in existence, please look for someone else to have that conversation.

"From your NYT piece: "Ten years in, the Large Hadron Collider has failed to deliver the exciting discoveries that scientists promised.". Was it a good investment then or did it fail? Do you not see how what you are saying is even more misleading to the public than the BSM predictions that failed to materialize?"

I meant exactly what I wrote. It failed to deliver evidence for BSM pheno. Does that mean the LHC was a bad investment? No it was not and I certainly did not say so. How about you stop fabricating opinions I do not hold and have certainly never voiced?

"Collider experiments have never been only about hacking off search space of BSM models. That you see it through that prism is..."

I did not say that is what collider experiments are all about. As I have said a seemingly endless amount of times, we had good motiviations (no BSM) to build colliders up to here. The Higgs was the last good motivation.

"Going directly to the media with your grievances is in my opinion harmful to science as whole..."

I did not "go directly to the media". I have previously written about problems in the field for Nature Physics, and also I have written about the problem for many years on this blog (so has Peter Woit on his blog). Oh, yeah, and I wrote a book too, almost forgot.

Also, if you think about it for a moment, do you really believe I got to write for the NYT just because I felt like it? How plausible does that sound?

The reason the NYT published my opinion piece is that this is a matter of public interest. Everyone who follows science news can recall the headlines about fancy things that the LHC was supposed to find. They noticed that didn't happen. They want to know what is going on. And it seems I am the only one willing to give straight answers.

"Also, your arguments for funding seem to boil down to the fact that you know better than funding agencies what is worthwhile and we should all just call you up for your gut feeling on whether something is "promising" rather than bother with 1000+ page reports on the physics case of an experiment."

I have delivered very clear arguments for why a larger collider is not currently a promising investment. You may not like those arguments, but at least I *do* have arguments. That's more than what can be said about particle physicists, who tend to think that "hey here is our 700 page report listing all the things we want to do with your tax money" suffices as an argument.

You and your particle physics friends mistakenly seem to think that I am the problem. But I am not the problem. I am merely the narrator. The real problem is that you don't want to understand the situation you are in.

You say that you have arguments and that we do not address them. Here are in order the various misleading or incorrect statements/arguments that you made that I have mentioned over our conversation and that you have not addressed:

* "There is currently no reason to think a larger particle collider will do anything besides measuring some constants to higher precision." => wrong

* "But this knowledge [Higgs] will tell us little new about the universe and it cannot be used to obtain further knowledge either." => misleading/probably wrong

* "Compare the expenses for CERN’s FCC plans to that of the gravitational wave interferometer LIGO. LIGO’s price tag was well below a billion US$. Still, in 1991, physicists hotly debated whether it was worth the money." => misleading

* "But this was not a situation in which “nothing until 15 orders of magnitude higher” was the most plausible case." => very probably wrong

* "A particle collider tells you more about particle collisions. We have found the Higgs, all right, but there is nothing you can do with the Higgs now other than studying it closer." => pretty misleading

* "That’s why high-precision measurements, like that of the muon g-2 or the electric dipole moment, are an alternative to going to higher energies." => wrong

* "What I have said is that particle colliders are extremely expensive and yet we have better reasons that something is to see with other experiments, so we should do those other experiments first." => misleading

* "If you look at the history of science breakthroughs came from resolving inconsistencies, either between theory and experiment or internal consistencies." => wrong

* "As a research area matures, experiments to probe new ground become more costly and take up more resources. "Just look" is no longer an option. We have to be careful to select what are the most promising experiments to make." => I don't see any evidence for this.

* "We have seen 40 years of null-results listening to people like you. According to my extrapolation, if we continue listening to people like you we will see more null-results." => this extrapolation is meaningless

* "That is, focus on studying cases where we already have discrepancies between theory and experiment. Or focus on cases where you have predictions based on the resolution of inconsistencies. This is what has historically worked. There isn't any such case for a larger collider at the moment." => wrong

As for the NYT: they love controversy and you have a lot of visibility and credibility with your blog. Don't worry though, your piece is in good company on their opinion page alongside these beautieshttps://www.nytimes.com/2017/04/28/opinion/climate-of-complete-certainty.htmlhttps://www.nytimes.com/2016/06/28/opinion/marine-le-pen-after-brexit-the-peoples-spring-is-inevitable.htmlhttps://www.nytimes.com/2016/05/01/opinion/sunday/donald-the-dove-hillary-the-hawk.html

Just repeating false arguments while ignoring my responses does not help your case:

"* "There is currently no reason to think a larger particle collider will do anything besides measuring some constants to higher precision." => wrong"

Then please deliver your killer-reasons. We are all holding our breath.

"* "But this knowledge [Higgs] will tell us little new about the universe and it cannot be used to obtain further knowledge either." => misleading/probably wrong"

So, yeah, how about you tell us what great things it'll do for us?

"But this was not a situation in which “nothing until 15 orders of magnitude higher” was the most plausible case." => very probably wrong

Says some commenter on my blog without giving any reasons. That's, erm, not very convincing.

I already said above, if you want to complain that it should be 13 rather than 15 orders of magnitude, because there are not entirely bad arguments new physics may appear already somewhat below the Planck scale that's fine. Let's talk about 13 orders of magnitude then.

"* "That’s why high-precision measurements, like that of the muon g-2 or the electric dipole moment, are an alternative to going to higher energies." => wrong"

Are you denying that high-precision measurements at low energy are sensitive to high-energy contributions?

"If you look at the history of science breakthroughs came from resolving inconsistencies, either between theory and experiment or internal consistencies." => wrong"

How about you list all the many breakthrough that did not come about because we discovered evidence that was incompatible with theory and then developed a new theory, or because we set out to probe a prediction based on resolving an inconsistency?

"As a research area matures, experiments to probe new ground become more costly and take up more resources. "Just look" is no longer an option. We have to be careful to select what are the most promising experiments to make." => I don't see any evidence for this."

Hard to see if you keep your eyes shut.

"We have seen 40 years of null-results listening to people like you. According to my extrapolation, if we continue listening to people like you we will see more null-results." => this extrapolation is meaningless"

Well, thanks for demonstrating that particle physicists are still in denial about what is going on.

"That is, focus on studying cases where we already have discrepancies between theory and experiment. Or focus on cases where you have predictions based on the resolution of inconsistencies. This is what has historically worked. There isn't any such case for a larger collider at the moment." => wrong"

If you think that's wrong, then please tell us what's the great reason to build the FCC? (And please spare us going on about some statistical fluctuations.)

"* "There is currently no reason to think a larger particle collider will do anything besides measuring some constants to higher precision." => wrong"

Then please deliver your killer-reasons. We are all holding our breath.

As I said before, it is wrong because a larger collider will measure new constants, not just improve present measurements. Perhaps you see it as semantics but I would disagree.

"* "But this knowledge [Higgs] will tell us little new about the universe and it cannot be used to obtain further knowledge either." => misleading/probably wrong"

So, yeah, how about you tell us what great things it'll do for us?

You say it as if it was already established fact that measurements of the Higgs won't tell us anything. It is not and perhaps we measure the trilinear coupling and we end up finding a 50% deviation from the SM, there is no way to know before measuring it. Even if we only find agreement, you say it like if it was a meaningless measurement. Would it be meaningless to measure the strong coupling constant for the first time?

"But this was not a situation in which “nothing until 15 orders of magnitude higher” was the most plausible case." => very probably wrong

Says some commenter on my blog without giving any reasons. That's, erm, not very convincing.

I already said above, if you want to complain that it should be 13 rather than 15 orders of magnitude, because there are not entirely bad arguments new physics may appear already somewhat below the Planck scale that's fine. Let's talk about 13 orders of magnitude then.

As I said in another of the points, it is in this case 11 not 13 or 15. In any case, extrapolating low energy effective theories too higher energies has rarely worked very well, so it would be amazing if the SM worked for another 11 orders of magnitude. I think most physicist would be very surprised, rather than finding this the most plausible scenario.

"* "That’s why high-precision measurements, like that of the muon g-2 or the electric dipole moment, are an alternative to going to higher energies." => wrong"

Are you denying that high-precision measurements at low energy are sensitive to high-energy contributions?

I am denying that they are cheap alternative. They are different experiments probing very specific things.

[cont'd]"If you look at the history of science breakthroughs came from resolving inconsistencies, either between theory and experiment or internal consistencies." => wrong"

How about you list all the many breakthrough that did not come about because we discovered evidence that was incompatible with theory and then developed a new theory, or because we set out to probe a prediction based on resolving an inconsistency?

As I said in a previous post, the discovery of the CMB, the proton, X-rays and radioactivity, for example, did not emerge from any inconsistencies in the theory, but were just unexpected findings that happened by doing measurements.

"As a research area matures, experiments to probe new ground become more costly and take up more resources. "Just look" is no longer an option. We have to be careful to select what are the most promising experiments to make." => I don't see any evidence for this."

Hard to see if you keep your eyes shut.

The world GDP is about 50 times what it was in 1940, 120 times what it was in 1820, so to first order, we can easily afford to make experiments that are proportionally more expensive.

"We have seen 40 years of null-results listening to people like you. According to my extrapolation, if we continue listening to people like you we will see more null-results." => this extrapolation is meaningless"

Well, thanks for demonstrating that particle physicists are still in denial about what is going on.

Here are another few data points from which you can do more meaningless extrapolations: colliders find on average >=1 new particles per generation; we have observed about 10 fundamental particles per order of magnitude below 1 TeV.

"That is, focus on studying cases where we already have discrepancies between theory and experiment. Or focus on cases where you have predictions based on the resolution of inconsistencies. This is what has historically worked. There isn't any such case for a larger collider at the moment." => wrong"

If you think that's wrong, then please tell us what's the great reason to build the FCC? (And please spare us going on about some statistical fluctuations.)

The part that is wrong is about "this is what has historically worked". Even if it was true, it is based on such a small sample size that extrapolating it is not a meaningful prediction.

I sincerely do not understand why you say I have not addressed your points. Please scroll up, I have offered very detailed responses to all of this already.

"it is wrong because a larger collider will measure new constants, not just improve present measurements. Perhaps you see it as semantics but I would disagree."

I am not sure just what the disagreement is here. Certainly we agree that without self-coupling the Higgs will not form a condensate?

"You say it as if it was already established fact that measurements of the Higgs won't tell us anything..."

I didn't say any such thing. I have gone to great pains to stress that it is very well possible that there is something new to find. I am not a prophet. The only thing I can say is that there is no reason to think there is something new to find.

"In any case, extrapolating low energy effective theories too higher energies has rarely worked very well, so it would be amazing if the SM worked for another 11 orders of magnitude."

The SM is renormalizable. There is no reason to think anything must happen in those 11 orders of magnitude.

"I am denying that they are cheap alternative. They are different experiments probing very specific things."

One can debate the meaning of "cheap" but largely I agree with that.

"As I said in a previous post, the discovery of the CMB, the proton, X-rays and radioactivity, for example, did not emerge from any inconsistencies in the theory, but were just unexpected findings that happened by doing measurements."

And I already responded to this saying that, yes, indeed those were experiment-led breakthroughs. We found an inconsistency between experiment and theory. We revised the theory. Progress followed. Hence, one of the avenues we should pursue is try to resolve inconsistencies between theory and experiment.

I believe (hope) this is a communication problem. Please read this to understand what I mean.

"The world GDP is about 50 times what it was in 1940, 120 times what it was in 1820, so to first order, we can easily afford to make experiments that are proportionally more expensive."

Just because we can afford doing something doesn't mean we should do it.

"Here are another few data points from which you can do more meaningless extrapolations: colliders find on average >=1 new particles per generation; we have observed about 10 fundamental particles per order of magnitude below 1 TeV."

And there is a good reason this extrapolation breaks down because the SM is complete and there is no reason to think any new physics will appear until somewhat below the Planck scale. We have already been through this.

Not sure what you were trying to say other than that you still haven't realized that the year is 2019, not 1999.

"this is what has historically worked". Even if it was true, it is based on such a small sample size that extrapolating it is not a meaningful prediction."

I certainly do not aspire to become a historian of science. But as I said, any argument is better than no argument.

"I am not sure just what the disagreement is here. Certainly we agree that without self-coupling the Higgs will not form a condensate? "

I am saying that measuring for the first time the coupling of the Higgs to a particle or to itself, or the branching ratio of a rare decay, is not measuring some constants to higher precision since they have not been measured yet. So your statement is incorrect.

"The only thing I can say is that there is no reason to think there is something new to find. [...] There is no reason to think anything must happen in those 11 orders of magnitude."

Yes, the same way Rutherford did not expect to see anything new beyond confirming the plum pudding model, yet measurements found something unexpected and our understanding of physics fundamentally changed.

"And I already responded to this saying that, yes, indeed those were experiment-led breakthroughs. We found an inconsistency between experiment and theory. We revised the theory. Progress followed. Hence, one of the avenues we should pursue is try to resolve inconsistencies between theory and experiment."

In the same vain as those discoveries, deviations in the Higgs sector would be an experiment-led breakthrough. I don't understand why you are obsessed with discoveries having to come from resolving inconsistencies between theory and experiment. Yes, this also happened in history and if we had clear indicators of some tension it would be nice. But it is not a necessary condition for discoveries, as history has shown many times.I don't think our disagreement is a communication problem.

"Just because we can afford doing something doesn't mean we should do it."

You say that we can not afford to "just look" anymore because it is becoming too expensive compared to earlier days of science. I am telling you that compared to 1820, we can afford to "just look" with experiments that are hundreds of times more expensive, because the world has also become much richer since then.

"And there is a good reason this extrapolation breaks down because the SM is complete and there is no reason to think any new physics will appear until somewhat below the Planck scale. We have already been through this."

Yes and you can still not explain neutrinos with the current standard model so this is still not true. Whether this is irrelevant for the FCC case does not make it any less incorrect.

As I already said elsewhere, measuring the self-coupling of the Higgs is the one good argument that particle physicists have for the FCC. Personally I doubt that this will be convincing enough to get $20B, especially not given the technological situation, but if particle physicists would just stick with that (and related measurement proposals) and drop nonsense arguments ("money is wasted elsewhere too!", "just look!", "dark matter!") that would be fine with me.

Having said this, I hope we agree that in the SM, the coupling constants you refer to are related to constants we already have constraints on. Hence I am saying you are measuring those constants to better precision rather than measuring new constants.

"In the same vain as those discoveries, deviations in the Higgs sector would be an experiment-led breakthrough. I don't understand why you are obsessed with discoveries having to come from resolving inconsistencies between theory and experiment..."

I am not "obsessed" with theory-led discoveries. I am afraid you are still missing the point. Yes, it is possible that the FCC would see something exciting and new. But the same thing can be said about any other experiment that improves on any existing measurement. It is not a discriminatory argument. It does not explain why the FCC is the best way forward. It is a vanilla-argument that says "keep on doing experiments". Well and fine. But it fails to explain why spend money on the FCC and not on some other experiment.

What I have been telling you is that our best shot at getting results rather than null-results is to either collect more details of already known discrepancies between experiment and theory ("experiment-led") or to focus on cases where we have predictions based on the resolution of internal theoretical inconsistencies.

I have already named current examples for both cases multiple times, but in case you have already forgotten, let me know and I will copy and paste it here.

"I am telling you that compared to 1820, we can afford to "just look" with experiments that are hundreds of times more expensive, because the world has also become much richer since then"

Yeah, great. I have no idea what you think I said about 1820. Really if you want to argue that we should build the FCC because we can, well, let me just say I don't think that argument will fly.

"Yes and you can still not explain neutrinos with the current standard model..."

Yes, you are right, sorry I forgot about this. But you know it anyway, and you also know that it doesn't make a difference for the argument, so really what's your issue other than that you like to complain? Best,

So sorry to see this debate going on like this. Sabine has only 24 hours a day. But the opposite side has how many man-hours? How unfair this debate or fight is! I feel like a spectator watching a lion surrounded by a pack of thousand hyenas. The lion is fierce and formidable, but how can it defend itself to the end when the hyenas are charging against the lion one after another (asking basically the same questions over and over again), waiting for missteps and gaps in its defense to bite off a chunk out of hind legs. What sort of ending do you expect? If I were Sabine, I would have had a severe nervous breakdown. What a brave human being she is!

Fx, and other simpathizers, instead of attacking Sabine here, why don't you make a case for building the next collider in news media? Why don't you write op-ed pieces in New York Times and persuade the public of the necessity to build the bigger and more powerful collider? This embittered responses to Sabine's opinion are in fact tarnishing the image of the whole particle physics community. Do the positive things as you criticize Sabine being negative, or go back to your den!

I fully agree. They all just demonstrate their panic and lack of safety. It's a great variant of "the emperor's new clothes". A mixture of anger and fear is present and cause a very defensive mode of action. This narrows down awareness and so they seem to not even see how they make Sabine's case just more clear by akting like this. Not to mention the damage they cause to their image and the relationship to the public - which is ridiculous since they whant public funding.

I'd like to add something else: Your picture of the fighting lion is strong and it could be seen as a metaphor for what is going on. Nevertheless, I think there is also another angle of view: Sabine successfully made these people act out and show their real affective state. With this, they show also how they really think about their relationship to society. I read comments here that contained statements that these people would normally never say in public - because normally they know how counterproductive this would be. But the heightened affective state and a lack of affect regulation makes them drop their masks. This is actually very valuable since it makes the broken relationship between these people and the public visible - to the public.

I am very thankful and I can't express how much ich appreciate Sabine's work and courage in this. She is doing a great service for the society and the respect that this deserves does not depend on how it finally ends.

Regarding the couplings, yes we have constraints because they are related in the SM, but I still think that your description is not fair. If you measure e.g. some rare decay of the Higgs to a meason and photon for the first time, it is still a first measurement, and before you do it the uncertainty bars are infinite, even if you have some expectation within the SM.

"Yes, it is possible that the FCC would see something exciting and new. But the same thing can be said about any other experiment that improves on any existing measurement."

In terms of "just looking", as you must know, one of the arguments of collider physics is that they allow us to "just look" for many things at once: if there is any kind of new physics in the 1 - 20 TeV range we have a very good chance of finding it. Most smaller scale experiments are not so versatile. Does this mean the FCC is the best way to find new physics? Maybe, maybe not, I have no idea. If I had to bet I would say probably we will discover something in some other way before, and if we are lucky the FCC can be used to probe it in more detail. Maybe we are not so lucky, and we only discover something much later, maybe we are even very unlucky and hep doesn't find any signal of anything for a generation. In any case, mapping the Higgs sector in detail is one of the few reliable things we can do, so we should do it.

"[...] our best shot at getting results rather than null-results is to either collect more details of already known discrepancies between experiment and theory ("experiment-led") or to focus on cases where we have predictions based on the resolution of internal theoretical inconsistencies. "

I think the root of our communication issue on this point is that I disagree with your characterization of "experiment-led", for example in the rutherford experiment I mentioned before, there was no discrepancy between the theory and experiment. There was a theory, it was tested by doing an experiment, it turned out to be wrong and we changed the theory to fit the data. This is what experiment-led means to me. The whole point of it is that there is no discrepancy until you do the measurement.I also don't think it is fair to say the FCC has the same chance of discovering new physics as any other experiment that improves measurements. Your prior expectation that the Higgs sector looks exactly SM-like seems to be very strong. I don't like to give probabilities but if I had to, I would probably take the bet at about even odds. For most experiments that probe one specific measurement, the odds are likely to be much much lower, because you can only explore something very limited.

"Yeah, great. I have no idea what you think I said about 1820. Really if you want to argue that we should build the FCC because we can, well, let me just say I don't think that argument will fly."

I don't think it is the strongest argument either, but when people say that we discovered something before by just looking and you reply to them that we can not afford to do that anymore because it has become too expensive, I just want to highlight the fact that in fact within 2-3 orders of magnitude, we actually can afford it just the same.

Jay,

Look, I am just some physicist that pretty much no one has heard of outside of my subfield, no one cares what I think and certainly the NYT would not publish my article. I do appreciate the fact that Sabine was willing to engage, even though I was quite combative. You also have to understand the fact that as far as I am concerned, I have spent the better part of the last decade working on collider physics and it is not very pleasant to be cast as a cash-grabbing scammer in a dead end field. Particularly because I really don't think this has any truth to it and I don't think Sabine has a very realistic view of what particle physics is about and what people like me or my experimentalist friends do and are trying to achieve.

I think I have no major disagreements with that, except for some semantic quibbles about just exactly what the FCC could measure. I get the impression we agree on the math but not on the phrasing.

As to me supposedly not having a "realistic view of what particle physics is about" and what "people like me... are trying to achieve", let me just say that I have almost certainly spent more time thinking about what you folks are trying to achieve than you did yourself. I am not surprised we are here today having this discussion. If you can maybe for a moment put aside your conviction that I have no idea what I'm doing or that I am pushing some secret agenda, you might understand where I am coming from. I'm not difficult to interpret and I have stated my position clearly.

Well I would say that semantics matter because by being a little bit sloppy here and there it is easy to paint a distorted picture. Limits at 10^15 GeV become the planck scale, the standard model becomes complete, reasonable arguments to do measurements of an unexplored sector of physics are compared to unrealistic expectations, you pick a few historical examples and modern experiments that prove your point while leaving out others that don't and slowly it becomes easier to say things are black and white, there is no good reason for particle physics anymore, every one in the field knows it but they are hiding these inconvenient truths. Things are not nearly as black and white as you depict them.

"let me just say that I have almost certainly spent more time thinking about what you folks are trying to achieve than you did yourself."

I believe I have been forthcoming with my explanations and have apologized in those cases where I unintentionally forgot to add qualifiers. There is only so much I can squeeze into one blogpost.

That you are now trying to discard everything I said because you found some phrasing to complain about, after I have explained the matter to you patiently over and over again, is intellectually dishonest and amounts to plain denial.

Furthermore, I never said anything about "unrealistic expectations" - this is something you just fabricated. Neither did I pick historical examples. I asked you to come up with a counterexample. Unsurprisingly, you didn't find one. You then merely insisted that you do not like the way I use the phrase "experiment-led". Since I find it moot to discuss definitions of words, I chose not to pursue the matter. In case you really still did not understand what I mean, please let me know, and I will be happy to explain it once again. But honestly I get the impression you merely pretend to not understand what I say because it doesn't suit your narrative.

You are right that I cannot know I have spent more time thinking about what's going on in your community than you did yourself. Neither for that matter, do you have any reason to think that you are the one with the more realistic view, as you stated so confidently.

Since this is a question we will not be able to resolve, let me just say that those who have read my book will recognize in this comment section the problems in your community that I have written about: Refusal to acknowledge that 40 years of wrong predictions followed by null-results are a problem that warrants attention, and a remarkable overconfidence bolstered by group-think that what you are doing is certainly the right thing and those who don't agree with you must be stupid.

„Refusal to acknowledge that 40 years of wrong predictions followed by null-results are a problem that warrants attention, and a remarkable overconfidence bolstered by group-think that what you are doing is certainly the right thing and those who don't agree with you must be stupid.“

I fully agree that this discussion thread (and some others on your blog from the past days) demonstrated the key problems from your book, especially the social ones. I must admit that I didn’t really expected it to be so strikingly clear to see.

What disturbed me most is not the strong defensiveness in the responses. I was prepared for that and have an idea for the underlying causes. But there were some arguments that are close to a defamation of the public: It was argued, that even if it were very unlikely that the FCC will really bring major new insights, it would still be ok to demand the billions for it - because the public is so dump that they would otherwise most likely invest it in useless things like weapons and war. Wow - and that in a publicly accessible forum. Who do these people think they are?

My personal impression is that you can see major arrogance up to narcissism behind such arguing. This really concerns me, especially in a time were science in general is increasingly attacked and denied. Such arguing contributes to erode the attachment between science and society.

I do not think that Pascal Häußler is an impartial observer. Moreover, I think that his comments are defamatory. He rephrases other peoples statements to make them look rediculous. For example, he claims that people that support the FCC wrote in the comments here that:

"the public is so dump that they would otherwise most likely invest it in useless things like weapons and war."

Nobody wrote any such thing. The closest thing I could find is someone that wrote that it is "possible that the money goes towards military spending". Claiming that our resources are not spend in an optimal way is very different from saying that "the public is so dump".

Then Pascal asks "Who do these people think they are?". These people are members of the public who are entitled to their own opinion just like you are. If the FCC is funded, I won't get a dime from it, directly or indirectly. Still, I hope that it will be funded in one variation or another.

Some people on both side of the argument used defamatory language. We should all discorage this behavior, be careful not to use such style ourselves, and try to keep the discussion civil and constructive.

I said he is impartial because I believe he has no stakes in whether or not the FCC will be built. (Neither, for that matter, have I, just for the record.)

In my impression he is simply reporting what impression particle physicists' public comments here and elsewhere give. He reports that their superficial argumentation leaves the impression that they must think the public is entirely dumb.

I am not sure that's right, but I can certainly see that one could have this impression.

Personally I suspect that most of them don't realize just how sloppy their arguments are. They merely repeat the arguments that everyone in their community has made for decades. That Prof Randall thinks the "money is wasted elsewhere too" argument would be good to bring up in a letter to the NYT, out of all places, and particle physicists then cheer for her awesome argument, tells you just how bad the group-think is in this community.

I did not rephrase anything. I did not use quotes to make it look like a citation. That is something you just invented.

There was (yes, was) a post containing a statement that said that is it ok to request the billions for the FCC even if it is very unlikely that anything essential will be discovered, because the silly public would use it otherwise for other useless things like weapons or war. I cite it from memory because it's lost. But it indeed didn't use the word "dump". But silly or dump does not make a big difference for me.

I learnd one thing from this: Comments can get deleted by their authors and with this, attached direct replies. I can't look it up anymore just as you. Also my direct reply is missing. Good to know: Don't use direct reply with serious things and quote everything critical directly in your own post.

"Comments can get deleted by their authors and with this, attached direct replies."

As someone kindly checked for me, what you say is not correct. If an author deletes a comment, this will leave an empty relic comment that says "comment deleted by author". This will not remove responses to the (no longer existing) comment.

Only blog "owners" can entirely delete comments (including responses, if those exist). I have not deleted any comments in this thread (except for some of my own comments that I resubmitted because they contained typos).

Indeed, since I have comment moderation on, I pretty much never delete other people's comments. If something seems inappropriate, I'll not publish it in the first place.

Pascal, this makes it very likely that you may have confused different comment sections or just couldn't find the comment you were looking for.

"I did not rephrase anything. I did not use quotes to make it look like a citation. That is something you just invented."

I didn't say that you misquoted someone, I said that you rephrased. You took some comment that maybe you heard someone said somewhere, you rephrased it and then you blame an entire group of people of having the same opinion. This is a perfect example of defamation.

I assume that this was not intentional and that it is just the impression that you got from reading about the subject. I urge you to reconsider the way you portray this community. Even if you do not agree with them, you should try to be more careful in the way you criticize them. Take an example from Sabine for how to do it professionally.

Do you realize how condescending it is to tell me, after I explained that I spent most of the last decade working solely on collider-related physics, that you have thought more carefully about my own field than me? and now you are calling me intellectually dishonest...

I came here because I saw a large number of statements that I considered misleading or wrong and I called you out on it. I do commend you a little bit for engaging but it doesn't change the fact that your posts are misleading.

About unrealistic expectations: when people tell you probing the Higgs is a pretty good way to look for new physics, you say there is no reason we will find anything - I think a few weeks ago I even saw you comparing the FCC to a car salesman promising a car that flies to the moon - then you say the last good prediction was the Higgs. Yes, the LHC had an extremely strong case because the Higgs, or something, had to be there, we can not always be so lucky when we design an experiment: it is not a realistic expectation.

About historical examples that you did not pick: maybe look at your own two figures above and the paragraph on LIGO, LISA and SKA and then tell me how you are not doing that. As for counter-example, I gave four examples earlier of discoveries that did not arrise from any inconsistencies with data or in the theory so I'm not sure where the problem is.

As for your last point, look I consider myself pretty reasonable and am more than willing to be challenged on what the best way forward is. Are we just in a plateau before a new era of discoveries or is the field slowly trailing towards a stale-mate? I don't know, and neither do you. If someone has a fantastic idea for a reliable way of testing new phenomena, and if we had to end up deciding between funding a collider or that new idea, I would say awesome, let's go for it. But I don't see you offering any better alternative, you are pretty much just saying lets kill the field and move on to something else.

I totally understand that you are offended, but really I don't see how that is relevant. You are part of a large community of people who almost exclusively talk among themselves. Your primary course of action is to keep on doing what you have been doing already. It's not only institutional inertia, it is also that you sincerely think that that's the only right thing to do. I am telling you it is time to look at the facts.

Your predictions for BSM physics have been wrong for 40 years. All experiments that looked for such physics delivered null-results. A new collider is costly, we have no reason to think it will bring anything but new null-results, and the technologies which may make colliders more efficient are not ready yet.

Investing in a larger collider at the present time makes no sense. Right now, we have more promising avenues to pursue.

That your community is unable to do as much as acknowledge that 40 years of wrong predictions even happened worries me a lot because this lack of self-reflection and self-correction is in the way of progress. Believe that or not, I have spent quite some time thinking about what is going on and what to do about it. I do not expect you or anyone else to agree with my analysis or my recommendation, but I do expect you to at least think about the matter and come up with your own conclusions.

"I even saw you comparing the FCC to a car salesman promising a car that flies to the moon"

Wot? I was commenting on a video about the FCC that is as truthful as a car salesman claiming a car will fly to the moon and back, a claim similarly accurate as saying that the FCC will tell us something about "origin of the universe". If this was a commercial video, consumer protection would take it down in no time. When scientists market their pet projects, apparently everything is allowed. I want people to know what is really going on. It is beyond me how such deliberate mis-information campaigns by tax-funded scientific institutions are even legal.

More seriously, what do you think you will achieve with this. Suppose you get funding for the FCC and in 30 years people will come and ask, so now what is the origin of the universe? What do you want to tell them?

"maybe look at your own two figures above and the paragraph on LIGO, LISA and SKA and then tell me how you are not doing that. As for counter-example, I gave four examples earlier of discoveries that did not arrise from any inconsistencies with data or in the theory so I'm not sure where the problem is."

You are confusing two different things, either deliberately or accidentally. I was asked (can't recall by whom) about other experiments that I think are well-motivated. I answered this question.

The other question was about counter arguments to me telling you that breakthroughs are either experiment-led (discrepancy between theory and experiment leading to a revision of theory) or theory-led (internal inconsistency in the theory leading to a prediction that is confirmed by theory). The supposed "counter-examples" you offer are cases of experiment-led breakthroughs. They are not counter-examples. I already told you this above. I also already told you above that in case you have trouble understanding what I am saying, please read this earlier post.

I do not understand why you repeat your wrong counter-examples after I have explained to you why they are wrong.

"If someone has a fantastic idea for a reliable way of testing new phenomena, and if we had to end up deciding between funding a collider or that new idea, I would say awesome, let's go for it. But I don't see you offering any better alternative, you are pretty much just saying lets kill the field and move on to something else."

This is badly misrepresenting my position. As I have repeated a seemingly endless amount of times, my point is not that colliders are somehow bad, but that a next larger collider is not currently the best way to invest money into progress in the foundations of physics. There are better things we could do with the money.

I have also listed dozens of times already what are better ways to invest the money. First, focus on resolving known discrepancies between experiment and data until you can update theory, thereby hopefully getting new predictions. Second, focus on resolving internal inconsistencies in the theories. These situations currently exist, for example, in dark matter observations (actual observations, not, as someone above mistakenly thought, the attempt to detect particles that may not exist), in quantum gravity or in quantum foundations. There is no such case in high energy particle physics at the moment.

Your statement that I am not offering better alternatives is therefore plainly wrong. I do not know why you are saying this after I have repeated so many times that the whole issue is that there are *better* things to do.

I think the comparison with LIGO shows exactly why the FCC is a bad investment. When LIGO was first proposed, the arguments against it was (a) It's not going to see anything at low sensitivities and (b) while we know that at high sensitivities, it should see things, it's going to be technologically impossible to increase the sensitivity to that extent.

The counterargument was that (a) we don't know it won't see something at low sensitivities, and (b) it is indeed technologically possible to increase the sensitivity so that it will see black hole mergers, which we know exist.

The critics were right about (a), but completely wrong about (b).

For the FCC, everybody agrees on (b) — you won't be able to increase the energy to the point where we know we will see something new. So you're stuck with argument (a), which for LIGO failed.

@sabine"More seriously, what do you think you will achieve with this. Suppose you get funding for the and in 30 years people will come and ask, so now what is ? What do you want to tell them?"

So, sabine, let's open a new blog to take down and de-fund ALL EU public research on cancer... 'cause it has been funded during way more than 30 years... for amounts way more than the anecdotal fraction-of-a-euro-per-EU-household-per-year estimated for the FCC.

"... and (b) it is indeed technologically possible to increase the sensitivity so that it will see black hole mergers, which we know exist."

That could be a good point, provided one specifies that if LIGO, VIRGO and most of all all future upgrades will be able to get to better sensitivities it will be thanks to research carried out for HEP colliders over the past 50 years. Just one example: if it were for industrial products not developed for HEP, there would be no way to make a vacuum good enough for the operation of the GW detectors, especially those under design now.Cheers.

I think we are slowly going in circles so apologies if I do not address all of your points.

Believe it or not I am not personally offended or angry or anything. But you say that you have thought more about my own field than me or my colleagues, yet I don't see anywhere any indication that you have any expertise in modern particle physics or even have anything past grad-student level understanding of my field. Having written a couple of BSM papers on LHC physics 15 years ago does not make you an authority on collider physics. I don't think you have any appreciation for, or even care about, why automated fixed order calculations were a significant breakthrough, how recent developments in amplitude calculations are paving the way for percent-level measurements and how these will feed back to improve our understanding of particle physics, why the diboson channel can be used in clever ways to do indirect measurements of the Higgs width, etc, etc. No one is an expert on everything, and you are certainly entitled to have views on the field regardless, but it is extremely arrogant to come here and tell us our field is not promising, without even making the effort of trying to understand what the field is about, by writing posts that are peppered with misrepresentations and half-truths.

"More seriously, what do you think you will achieve with this. Suppose you get funding for the FCC and in 30 years people will come and ask, so now what is the origin of the universe? What do you want to tell them?"

I think the FCC is well motivated because regardless of whether we find new physics or not, we can use it to map out the Higgs sector. If in 30 years we end up finding new physics within reach, then this will be sufficient motivation to continue doing experiments. If we come to realize that there is no new fundamental particles below 10^5 TeV or something, then I think there is not much point anymore in building another, even larger, collider.

"The supposed "counter-examples" you offer are cases of experiment-led breakthroughs."

Maybe I misunderstand you but I don't see how the Rutherford experiment or the CMB discovery were experiment-led in the way you mean it, there was no disagreement between theory and experiment before the experiment was done, we just did a measurement that could not be explained by the current theory and it led to a breakthrough. In the same way, if we measure some Higgs coupling and it deviates from the SM, it will lead to a breakthrough or revision of our understanding.

"As I have repeated a seemingly endless amount of times, my point is not that colliders are somehow bad, but that a next larger collider is not currently the best way to invest money into progress in the foundations of physics. There are better things we could do with the money."

All of the things you list are being actively pursued and if there is anything to be found there, it will be found, probably much before we build a new collider. They are also not alternatives, they are completely different subfields. None of them would allow us to study the Higgs sector. With pretty much the same argument I can say quantum gravity is not currently a promising avenue for humanity to spend resources on, let's invest that money in building better generative adverserial networks instead, it is a much more promising avenue to focus on.

It is correct that I am not an expert on the recent developments in particle physics. Neither did I pretend to be one. Your questioning my expertise rather than my argument is also irrelevant to the discussion and constitutes an ad hominem attack.

"it is extremely arrogant to come here and tell us our field is not promising"

I did not say anything like this. I said very clearly and very specifically that investing in a next larger collider is not currently a promising route to progress in the foundations of physics. That you misconstrue this into me saying that particle physics isn't promising is a straw man argument. It documents your unwillingness to think about what I am saying.

"Maybe I misunderstand you but I don't see how the Rutherford experiment or the CMB discovery were experiment-led in the way you mean it, there was no disagreement between theory and experiment before the experiment was done"

You do not need a disagreement between theory and experiment before the experiment was done to have an experiment-led breakthrough. This does not make any sense. A breakthrough is experiment-led if the experiment discovers a discrepancy between an existing theory and measurement and the theory has to be revised. (Or, if no theory exists, a new has to be developed.)

Let me just guess here that the reason for your misunderstanding is that you think me saying we should focus on existing discrepancies between theory and data (besides internal consistencies) refers to "experiment led". This is not so. A "just look" search would also be "experiment led". What I am saying is that "just look" has not worked for the past 40 years. We should draw consequences and be more careful about deciding where to look. Hence, focus the experiment-led explorations on those cases where we already know discrepancies.

To say this once again differently. I do not say, and have never said, that this is what has been done previously. Instead, as I stress in my book, the more difficult it becomes to test new regions of parameter space the more careful we have to be when deciding what to test.

"They are also not alternatives, they are completely different subfields..."

You cannot on the one hand argue that the FCC is supposed to look for dark matter and dark energy and tell you something about the early universe and baryon asymmetry, and maybe about grand unification and extra dimensions, but on the other hand pretend that this is completely different than what astrophysicists, cosmologists, and people in quantum gravity are trying to do.

"None of them would allow us to study the Higgs sector."

That's right. As I said, that's the one reasonable point that you have. I suggest you stick with that.